微调更新的秩度量需要噪声基线

# Rank Measures of Fine-Tuning UpdatesNeed a Noise Baseline
Source: [https://arxiv.org/html/2610.22438](https://arxiv.org/html/2610.22438)
###### Abstract

Studies of what fine\-tuning does to a language model often summarise the weight updateΔ​W\\Delta Wby its rank\. We compare the rank measures used for this against the same measures on a random matrix of the same shape, and against two harder references: the pretrained weights, and matched fine\-tunes without alignment content\. Measures that count directions put our fine\-tuning updates only a little below noise; stable rank, computed from the same singular values, puts them far below\. Both are right: an update has a few strong directions on top of a long tail\. The pattern holds for thirteen released pairs up to 8B parameters, and it is not a mark of alignment: with training held fixed, instruction data does not stand out from Wikipedia or code, DPO gives the same update whether its preference labels are real or half swapped at random \(one model, modest preference strength\), and scrambled text gives the most concentrated update of all\. Applied to a recent claim that post\-training is superficial because the effective rank of the weights barely changes, the baselines show that a random update of the same size leaves that rank almost unchanged while wrecking the model, and that an edit built on the effective rank of the update has no measurable effect in our tests\. Rank measures of weight updates need a noise baseline, and claims about alignment need a control without alignment content\.

## 1Introduction

When a language model is fine\-tuned, each weight matrixWWchanges by an updateΔ​W\\Delta W\.111Large language model tools were used to assist with editing the prose and with writing analysis code; all ideas, experiments, analyses and claims are the author’s own\.A natural way to ask what fine\-tuning did is to ask how many independent directionsΔ​W\\Delta Wuses, that is, its rank\. A low\-rank update suggests a small, targeted change; a full\-rank one suggests a diffuse change\.

The question matters most for alignment\. The superficial alignment hypothesis\([Zhou et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib1)\)holds that alignment mostly teaches a model which style to answer in, and output\-level evidence supports it\([Lin et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib2)\)\. If that is true, one might expect alignment to leave a small, structured footprint in the weights, and recent work has looked for one in the rank ofΔ​W\\Delta Wand ofWW\([Wu et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib3)\)\. Related work reports that fine\-tuning updates are “high rank”\([Biderman et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib12)\)or “nearly full\-rank”\([Mukherjee et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib19)\)\.

Real updates are full rank in the strict sense, so these readings rest on softer measures: the numerical rank, the number of directions that hold 90% of the energy\([Biderman et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib12)\), or the entropy effective rank\([Roy and Vetterli, 2007](https://arxiv.org/html/2610.22438#bib.bib29);[Wu et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib3)\)\.[Biderman et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib12)also compared against noise: the spectrum of a fully fine\-tuned weight matrix looks like that of the pretrained one plus low\-magnitude Gaussian noise, and they concluded that nothing about it is unusual\. We began this project with the same impression\. Counting the singular values of a supervised fine\-tuning \(SFT\) update above 1% of the largest gave 97% of full rank, and the difference between two random initialisations of the same model, which is pure noise, gave 99\.6%\. By that measure, fine\-tuning looks almost like noise\.

It is not\. Stable rank\([Rudelson and Vershynin, 2007](https://arxiv.org/html/2610.22438#bib.bib30)\), computed from the same singular values, puts the update 4\.5 times below noise, and its top direction holds 6\.6 times as much of the energy \(4\.2% against 0\.6%\)\. The two answers differ because the measures weigh different parts of the spectrum, and because measures ofWWcannot see much ofΔ​W\\Delta Wat all\. Comparing against noise is an old idea in statistics\([Horn, 1965](https://arxiv.org/html/2610.22438#bib.bib31);[Gavish and Donoho, 2014](https://arxiv.org/html/2610.22438#bib.bib32)\), has been used to study trained weights\([Martin and Mahoney, 2021](https://arxiv.org/html/2610.22438#bib.bib33);[Thamm et al\., 2022](https://arxiv.org/html/2610.22438#bib.bib34)\), and has been applied to fine\-tuning updates before:[Ryu et al\. \(2023\)](https://arxiv.org/html/2610.22438#bib.bib16)plot the spectrum of an update against a Marchenko–Pastur reference, and[Biderman et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib12)against Gaussian noise\. What has not been done is to apply it measure by measure, which is where the disagreement is, with matched controls for what the update was trained on\. That is what this paper does\.

Our findings:

1. 1\.Counting measures compress the gap to noise\.On our SFT, Wikipedia, code and direct preference optimisation \(DPO\) fine\-tunes, the threshold count is only 2–5% below a random matrix of the same shape, and eRank and the 90% energy rank are 12–35% below it; stable rank is 78–94% below\. Along the whole family of Rényi ranks the gap grows with how much weight a measure gives to the top directions, then levels off, as it must for any spectrum with a heavier head than noise; the point is how large the disagreement is \(§[4\.1](https://arxiv.org/html/2610.22438#S4.SS1)\)\.
2. 2\.Updates have a few strong directions and a long tail, and on average are more concentrated than the pretrained weights they are added to \(§[4\.2](https://arxiv.org/html/2610.22438#S4.SS2)\)\.
3. 3\.The shape does not single out alignment training\.With the amount of training held fixed, the data does shape an update \(code is the least concentrated, the more so with more training\), but instruction SFT does not stand out from Wikipedia or Python code\. DPO gives the same shape, and the same directions, whether it learns real preferences or randomly swapped ones that teach nothing\. Text with its word order scrambled gives the most concentrated update of all \(§[4\.3](https://arxiv.org/html/2610.22438#S4.SS3)\)\.
4. 4\.It holds for released models, thirteen base/instruct, post\-training\-stage and base/specialist pairs up to 8B parameters\. On three bf16 updates \(Qwen2\.5\-1\.5B and the OLMo 2 DPO and RL stages\), much of what the threshold count counts may be rounding \(§[4\.4](https://arxiv.org/html/2610.22438#S4.SS4)\)\.
5. 5\.It changes how earlier evidence reads\.An unchanged effective rank ofWWafter post\-training, read by[Wu et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib3)as a sign that post\-training is superficial, is what a random update of the same size also produces, even one that cuts the model’s GSM8K accuracy from 60% to 5%\. The edit they build on the effective rank of the update has no measurable effect on GSM8K, nor, within about three points, on their own benchmark, GPQA\-Diamond \(§[5](https://arxiv.org/html/2610.22438#S5)\)\.

The practical message is short: report rank measures of weight updates next to the same measure on noise, check that low\-precision training or storage did not erase the update, and test claims about alignment against fine\-tuning without alignment content\.

## 2Measuring the rank of an update

LetΔ​W∈ℝm×n\\Delta W\\in\\mathbb\{R\}^\{m\\times n\}be the update to one weight matrix,r=min⁡\(m,n\)r=\\min\(m,n\), andσ1≥⋯≥σr\\sigma\_\{1\}\\geq\\dots\\geq\\sigma\_\{r\}its singular values\. Writepi=σi2/∑jσj2p\_\{i\}=\\sigma\_\{i\}^\{2\}/\\sum\_\{j\}\\sigma\_\{j\}^\{2\}for the share of the update’s energy \(squared Frobenius norm\) in directionii\. We report every measure as a fraction ofrr, so that matrices of different shapes can be averaged\.

##### Five measures\.

In plain words, each asks “how many directions does this update really use?”, and they differ in how much the strongest directions count\.

- •Threshold countρ0\.01\\rho\_\{0\.01\}: how manyσi\\sigma\_\{i\}are at least0\.01​σ10\.01\\,\\sigma\_\{1\}\. We use it as the simplest example of counting; the numerical rank reported by[Mukherjee et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib19)counts in the same way, with a tolerance they do not state \(by default it is set by floating\-point precision\)\.
- •Energy rankk0\.9k\_\{0\.9\}: the smallestkkwith∑i≤kpi≥0\.9\\sum\_\{i\\leq k\}p\_\{i\}\\geq 0\.9, the measure of[Biderman et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib12)\.
- •Entropy effective rankeRank\\mathrm\{eRank\}\([Roy and Vetterli, 2007](https://arxiv.org/html/2610.22438#bib.bib29)\):exp\(−∑iqilogqi\)\\exp\\bigl\(\-\\sum\_\{i\}q\_\{i\}\\log q\_\{i\}\\bigr\)withqi=σi/∑jσjq\_\{i\}=\\sigma\_\{i\}/\\sum\_\{j\}\\sigma\_\{j\}, as used by[Wu et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib3)\.
- •Participation ratio:1/∑ipi21/\\sum\_\{i\}p\_\{i\}^\{2\}\.
- •Stable ranksr\\mathrm\{sr\}\([Rudelson and Vershynin, 2007](https://arxiv.org/html/2610.22438#bib.bib30)\):‖Δ​W‖F2/‖Δ​W‖22=1/p1\\\|\\Delta W\\\|\_\{F\}^\{2\}/\\\|\\Delta W\\\|\_\{2\}^\{2\}=1/p\_\{1\}\.

All five ignore the overall scale ofΔ​W\\Delta W\(they are scale\-invariant\), which matters because the updates we compare differ in size by orders of magnitude\.

##### How the measures relate\.

Three of the five are effective ranks of one kind: the exponential of a Rényi entropy ofppof orderα\\alpha,Rα=\(∑ipiα\)1/\(1−α\)R\_\{\\alpha\}=\\bigl\(\\sum\_\{i\}p\_\{i\}^\{\\alpha\}\\bigr\)^\{1/\(1\-\\alpha\)\}\. Order 0 counts the nonzero directions \(the threshold count is a thresholded version of it\), order 2 is the participation ratio, and order∞\\inftyis the stable rank\. The higher the order, the more the top directions dominate\. This is why the measures can disagree about the same matrix: a spectrum with a few strong directions and a long tail of weak ones has many directions to count but most of its weight on top\. The other two are close relatives rather than members: eRank uses the Shannon entropy ofq∝σq\\propto\\sigmainstead ofp∝σ2p\\propto\\sigma^\{2\}, and the energy rank counts directions up to a fixed share ofpp\. We list them between the threshold count and the participation ratio, which is where their values fall for our updates\.

Note thatRαR\_\{\\alpha\}can only fall asα\\alphagrows, for any matrix, so the order of the raw values tells us nothing\. What does carry information is how far each measure puts an update below noise\.

##### The gap to noise\.

For each measure we report1−x¯update/x¯noise1\-\\bar\{x\}\_\{\\text\{update\}\}/\\bar\{x\}\_\{\\text\{noise\}\}, wherex¯\\bar\{x\}is the mean of the measure over all matrices of a model, whatever their shape: 0 means the update looks like noise, and values near 1 mean it is far more concentrated\. \(The noise value itself depends on the shape, from 0\.25 to 0\.53 for stable rank, Table[10](https://arxiv.org/html/2610.22438#A2.T10); Table[11](https://arxiv.org/html/2610.22438#A3.T11)gives the values by matrix type\.\) Intervals come from a bootstrap over layers \(§[3](https://arxiv.org/html/2610.22438#S3)\), and ratios quoted in the text, such as “4\.5 times below noise”, use the unrounded means\. The measures have different ceilings \(the threshold count of noise is already 0\.996\), so the gap is best compared across updates for one measure, and only roughly across measures\.

##### The noise baseline\.

A value of any of these measures only means something next to its value for a matrix with no structure\. For our own runs the baseline is the difference between two independent random initialisations of the same model; for released models, one Gaussian draw for each matrix, with the same shape\. The spectrum of such a matrix follows the Marchenko–Pastur law, whose upper edge \(the Bai–Yin limit,[Bai and Silverstein, 2010](https://arxiv.org/html/2610.22438#bib.bib37)\) gives a stable rank close to

m​n\(m\+n\)2,\\frac\{mn\}\{\(\\sqrt\{m\}\+\\sqrt\{n\}\)^\{2\}\},a quarter ofrrfor square matrices\. Our random\-init pairs match this to within 0\.01 for every matrix shape of Qwen2\.5\-0\.5B \(Table[10](https://arxiv.org/html/2610.22438#A2.T10)in Appendix[B](https://arxiv.org/html/2610.22438#A2)\), and the two baselines agree: on Qwen2\.5\-0\.5B the stable rank is 0\.436 for the random\-init pair and 0\.434 for the Gaussian matrices\.

Beating this baseline is necessary but not sufficient\. A Gaussian matrix is the least structured baseline possible, and any difference between two trained matrices beats it: the pretrained weightsWWthemselves have a stable rank well below noise, and so does the difference between two*unrelated*trained checkpoints \(§[3](https://arxiv.org/html/2610.22438#S3)\)\. The noise value tells the reader how to read a number; it does not by itself show that an update is special\. So we use two further references: the pretrained weightsWW, and fine\-tunes on data with no alignment content, trained the same way \(§[4\.3](https://arxiv.org/html/2610.22438#S4.SS3)\)\.

##### The rounding floor\.

Released checkpoints are usually stored in bf16, which rounds every weight to 8 significant bits\. The rounding adds a small noise matrix toΔ​W\\Delta W\. For each released pair we simulate it \(uniform error up to half a bf16 unit at each weight, independently for both checkpoints\)\. By Weyl’s inequality, rounding cannot create a direction ofΔ​W\\Delta Wstronger than its own largest singular value, so we report the share of the update’s singular values above that “rounding floor”\. The simulation is a generous model of rounding: when a weight barely moves, its two rounding errors are not independent, and the stored difference is exactly zero\. So we also report the direct evidence, the share of entries ofΔ​W\\Delta Wthat are exactly zero, meaning that the two checkpoints store the identical bf16 value\.

##### Measures ofWWrather thanΔ​W\\Delta W\.

Some studies measure the full weight matrix before and after fine\-tuning\. By Weyl’s inequality\([Horn and Johnson, 2012](https://arxiv.org/html/2610.22438#bib.bib38)\), each singular value ofW\+Δ​WW\+\\Delta Wis within‖Δ​W‖2\\\|\\Delta W\\\|\_\{2\}of the corresponding one ofWW\. When the update is small compared withWW, the large singular values ofWWbarely move; the small ones can move more relative to their size, so the bound alone does not settle how much a measure ofWWcan change\. We therefore test it directly against a random update of the same size,W\+G​‖Δ​W‖F/‖G‖FW\+G\\,\\\|\\Delta W\\\|\_\{F\}/\\\|G\\\|\_\{F\}withGGGaussian\.

## 3Setup

##### Our fine\-tunes\.

We fine\-tune Qwen2\.5\-0\.5B base\([Qwen Team, 2024](https://arxiv.org/html/2610.22438#bib.bib41)\)and SmolLM2\-360M base\([Ben Allal et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib43)\), all parameters, four ways each, with the same optimizer settings and the same number of training tokens \(about 1\.75M for Qwen and 1\.9M for SmolLM2 per epoch, counted after truncation, for three epochs\):

- •SFTon 10k instruction examples from Alpaca\-cleaned, a community\-cleaned version of Alpaca\([Taori et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib49)\), with the loss on answer tokens only;
- •wikitext: plain language\-model training on wikitext\-103\([Merity et al\., 2017](https://arxiv.org/html/2610.22438#bib.bib50)\), a corpus of Wikipedia articles;
- •code: the same on deduplicated Python files from CodeParrot\([CodeParrot, 2022](https://arxiv.org/html/2610.22438#bib.bib51)\);
- •shuffled words: the same wikitext documents with the word order scrambled inside each document, so the words and their frequencies are unchanged but there is no structure left to learn\.

SFT, wikitext and code were each run twice on both models, and DPO \(§[4\.3](https://arxiv.org/html/2610.22438#S4.SS3)\) twice on Qwen, with a different seed and a different data sample each time\. Matching tokens does not match optimizer steps: Python files are long, so the code runs take about 700 steps against about 1,850 for SFT and 1,900–2,100 for wikitext and shuffled words\. A further code run on each model matches the steps of SFT instead, at the cost of 2\.5–2\.7 times more code tokens\. Appendix[A](https://arxiv.org/html/2610.22438#A1)lists every setting \(Table[7](https://arxiv.org/html/2610.22438#A1.T7)\) and the steps, loss and update size of every run \(Table[8](https://arxiv.org/html/2610.22438#A1.T8)\)\.

##### Precision\.

All runs fit on one 6 GB GPU\. The weights are kept in fp32 and only the compute runs in bf16, with 8\-bit AdamW\([Dettmers et al\., 2022](https://arxiv.org/html/2610.22438#bib.bib39)\)and gradient checkpointing\([Chen et al\., 2016](https://arxiv.org/html/2610.22438#bib.bib40)\)\. This matters: if the weights themselves are stored in bf16, any update smaller than half a bf16 unit is rounded away\([Zamirai et al\., 2020](https://arxiv.org/html/2610.22438#bib.bib28);[Zhu et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib20)\)\. In a first round of our own runs that did exactly this, 77–98% of the weights never changed, and the measured “update” was an artefact of the rounding\. Every run reported here is checked after training: at most1\.01×10−51\.01\\times 10^\{\-5\}of the weights are unchanged\. We recommend this check to anyone measuring fine\-tuning updates\.

##### Released models\.

We measure thirteen official pairs with no training, in three groups\. \(i\) Base/instruct releases: SmolLM2 135M, 360M and 1\.7B; Qwen2\.5 0\.5B and 1\.5B; Qwen3 0\.6B and 8B\([Yang et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib42)\), the two Qwen3 pairs being among those studied by[Wu et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib3)\. \(ii\) The three post\-training stages of OLMo 2 1B\([Team OLMo et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib44)\), base to SFT, SFT to DPO and DPO to reinforcement learning \(RL\), whose training data is public\. \(iii\) Large updates without alignment content: Qwen2\.5\-Math\-1\.5B\([Yang et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib46)\)and Qwen2\.5\-Coder 0\.5B and 1\.5B\([Hui et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib45)\)against their bases\.

Before measuring a pair we check that the second checkpoint descends from the first: the cosine between the two sets of weights is 0\.99 or more for all seven base/instruct pairs and the OLMo stages, and 0\.20–0\.60 for the specialists, which were trained on far more data\. The check matters\. The released OLMo 2 1B SFT checkpoint \(revision0d85a3d\) has cosine 0\.00 with the main revision of the released base model \(a1847df\), over all 112 matrices: the two do not even share an initialisation\. The base model’s mid\-training checkpoints are published as branches\. The final checkpoint of the third mid\-training run \(stage2\-ingredient3\-step23852\-tokens51B, revisionf83cd64\) has cosine 0\.995 with the SFT model; the first two runs, which the model card describes as exploratory, reach 0\.991\. For the 1B model only the third run was used, with no merging, so we take its final checkpoint as the base of the SFT stage\. The difference between the unrelated pair still looks like a fine\-tuning update: its stable rank is 0\.077 against 0\.336 for noise, 4\.4 times below, close to the 0\.080 of the real SFT update\. The model card does not explain the difference, and we have not confirmed its cause with the maintainers; we report what the public checkpoints contain\.

##### What we measure\.

We measure every attention and MLP projection \(q,k,v,o,gate,up,down\): 168 matrices per Qwen2\.5\-0\.5B model, up to 252 for Qwen3\-8B\. Embeddings and the output head are excluded\. We report means over matrices\. Matrices in the same layer are not independent, so 95% intervals come from a bootstrap that resamples whole layers, and comparisons between runs on the same model are paired matrix by matrix\. These intervals describe the spread over layers within one run, not the variation between training runs; for that we have the second seeds\.

## 4What the rank measures say

### 4\.1Counting measures compress the gap to noise

Table 1:Rank measures as a fraction of the maximum rank, and the share of energy in the top direction, averaged over all attention and MLP matrices\. “Noise” is the random\-init pair; “pretrainedWW” is the base model’s own weights\. The DPO updates are measured from the SFT model they start from\.Figure 1:How far below noise each measure puts each update,1−update/noise1\-\\text\{update\}/\\text\{noise\}, with 95% layer\-bootstrap intervals\. Measures are ordered by how much weight they give to the top directions\. The gap grows from a few percent for the threshold count to 78–94% for stable rank, and to 90–97% for the shuffled\-words updates\.Table[1](https://arxiv.org/html/2610.22438#S4.T1)gives the five measures for our updates\. By the threshold count, the Qwen SFT, wikitext and code updates are at 97% of full rank, close to the 99\.6% of noise\. Stable rank tells a different story: every update is several times below noise, 4\.5 times for the Qwen SFT update, 10 to 17 times for the SmolLM2 updates, and up to 39 times for shuffled words\.

Figure[1](https://arxiv.org/html/2610.22438#S4.F1)shows how the measures fit together\. Ordered from the threshold count to stable rank, each measure puts the updates further below noise: about 2% for the threshold count, 12% for eRank, 25% for the 90% energy rank, 50% for the participation ratio and 78% for stable rank on Qwen, and the same order on SmolLM2\. The values for noise fall along the same order, and what grows is the distance between update and noise\. Along the whole family of Rényi ranks the gap grows steadily with the order, then levels off \(Figure[6](https://arxiv.org/html/2610.22438#A2.F6)in Appendix[B](https://arxiv.org/html/2610.22438#A2)\)\. This is expected for any spectrum with a heavier head than noise, so we read it less as a finding than as a warning: the answer depends on which order one happens to pick\. Every interval excludes zero, so all five measures do detect that the updates are not random\. The problem is the size of the gap\. The two measures used in the literature, eRank and the energy rank, put the SFT, wikitext, code and DPO updates 12–18% and 24–35% below noise; stable rank puts them 78–94% below\. The threshold count is also arbitrary: at0\.1​σ10\.1\\,\\sigma\_\{1\}instead of0\.01​σ10\.01\\,\\sigma\_\{1\}the Qwen SFT update sits 18% below noise instead of 2% \(Table[9](https://arxiv.org/html/2610.22438#A2.T9)\)\. A reader who sees “97% of full rank” without the noise value next to it will conclude that the update is diffuse, which is what we concluded at first\. The same holds for every matrix type \(Table[11](https://arxiv.org/html/2610.22438#A3.T11)\)\.

### 4\.2A few strong directions and a long tail

Figure 2:Where the energy sits, averaged over the 168 matrices of Qwen2\.5\-0\.5B\. Left: share of energy in the top fraction of directions\. Right: singular values relative to the largest\. Updates put much more energy in their top directions than noise does, then decay slowly over a long tail\. The pretrained weights \(dashed\) sit between the updates and noise\.Figure[2](https://arxiv.org/html/2610.22438#S4.F2)shows why the measures disagree\. At the top of the spectrum the updates are far more concentrated than noise: the top direction of the Qwen SFT update holds 4\.2% of its energy against 0\.6% for noise\. Below that the spectrum decays slowly, and this long tail still holds most of the energy\. Stable rank is dominated by the top, so it sees the concentration; the counting measures count directions, most of which are in the tail, so they see a nearly full\-rank matrix\. Both descriptions are true of the same matrix: fine\-tuning updates are high rank\([Biderman et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib12)\)and they are concentrated\. Long\-tailed update spectra have been noted before, in work on compressing updates\([Ping et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib15)\); what the noise baseline adds is how far from random the head of the spectrum is\. Nor is the result driven by one outlying direction: without the top direction, stable rank is 0\.126 for the Qwen SFT update against 0\.440 for noise \(Table[8](https://arxiv.org/html/2610.22438#A1.T8); the noise value is in Appendix[A](https://arxiv.org/html/2610.22438#A1)\)\.

The pretrained weights are a harder reference than noise, since they are themselves far from random, and the updates are more concentrated than them too, on average\. The stable rank of the pretrained weights is 0\.178 on Qwen and 0\.140 on SmolLM2, against 0\.093–0\.097 and 0\.020–0\.034 for the SFT, wikitext and code updates: 46–48% below the weights on Qwen and 75–86% on SmolLM2, with layer\-bootstrap intervals well clear of zero\. This does not hold for every matrix type: on Qwen, for thedownprojection, the SFT update and the weights are level \(Table[11](https://arxiv.org/html/2610.22438#A3.T11)\)\. The threshold count cannot see the difference either: it puts the Qwen updates and the pretrained weights at the same 97–98%\.

### 4\.3Instruction and preference training leave no special mark

Table 2:Differences in stable rank between runs on the same model, paired matrix by matrix, with 95% layer\-bootstrap intervals\. The intervals describe the spread over layers within one run, not between training runs; “second seed” repeats a run with a different seed and data sample\. “Steps matched” trains on code for as many optimizer steps as SFT, which is 2\.5–2\.7 times more code tokens\.A concentrated SFT update says nothing about instruction tuning unless fine\-tuning on other data looks different\. With the model, optimizer and number of training tokens held fixed, SFT does not stand out\. On Qwen, SFT, wikitext and code give stable ranks of 0\.097, 0\.093 and 0\.094; every paired difference between them is under 0\.005 and its interval includes zero \(Table[2](https://arxiv.org/html/2610.22438#S4.T2)\), and a second seed moves each by at most 0\.0014\. On SmolLM2 the data does leave a mark: code is the least concentrated \(0\.034\), wikitext the most \(0\.020\) and SFT sits between them \(0\.025\)\. These differences are real, not seed noise: a second seed of each SmolLM2 run moves its stable rank by at most 0\.0003\. Nor are they an artefact of the code runs taking 2\.6–2\.7 times fewer optimizer steps than SFT \(§[3](https://arxiv.org/html/2610.22438#S3)\): training on code for as many steps as SFT, which is 2\.5–2\.7 times more code tokens, moves the code update further from SFT, not closer, on both models \(stable rank 0\.114 on Qwen, 0\.042 on SmolLM2\)\. So what the data teaches, and how much of it, does shape the update\. What it does not do is single out instruction tuning: in both models SFT does not stand out from the ordinary language\-model runs\.

Similar stable rank means a similar spectral shape, not the same update, so we also compared the directions\. For each pair of runs we measured the overlap of the top\-16 left singular subspaces of each matrix’s update, averaged over matrices \(1 would be identical subspaces; two random subspaces give 0\.02–0\.04; Appendix[F](https://arxiv.org/html/2610.22438#A6)\)\. Two runs on the same kind of data with different seeds overlap by 0\.26–0\.32 on Qwen and 0\.34–0\.51 on SmolLM2\. Runs on different data overlap less, 0\.20–0\.22 on Qwen and 0\.12–0\.13 on SmolLM2, but still four to six times more than random\. So the data steers which directions an update uses, more than it changes the update’s shape\.

Preference training gives the same answer\. Starting from the Qwen SFT model, we ran DPO\([Rafailov et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib7)\)on 10k UltraFeedback pairs\([Cui et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib8)\), and a control on the same pairs with chosen and rejected swapped in a random half of them, in the spirit of random\-label controls\([Zhang et al\., 2017](https://arxiv.org/html/2610.22438#bib.bib9)\)\. The prompts, responses and amount of training are identical, but there is no net preference to learn; the control does share the unswapped half of its pairs with the DPO run, so it removes the preference signal, not everything the two runs see in common \(Appendix[A](https://arxiv.org/html/2610.22438#A1)\)\. On about 190 held\-out pairs the DPO model prefers the chosen answer 65% of the time \(74% for a second seed\); the control is at chance, 51%\. Yet the two updates are alike on every measure \(Table[1](https://arxiv.org/html/2610.22438#S4.T1)\): stable rank 0\.053 for DPO and 0\.055 for the control, against 0\.436 for noise, and the two updates have the same size \(Table[8](https://arxiv.org/html/2610.22438#A1.T8)\)\. The paired difference,\+0\.002\+0\.002, is larger than the gap between the two DPO seeds \(\+0\.001\+0\.001\) but under 4% of the value and about1/2001/200of the distance to noise \(Table[2](https://arxiv.org/html/2610.22438#S4.T2)\)\. The directions agree too: the real DPO update overlaps with the swapped control \(0\.27\) almost exactly as much as with a second seed of itself \(0\.28\)\. Like the SFT update, the DPO update is more concentrated than the pretrained weights and far more than noise, and at the strength of preference learning we reach, almost none of that, in shape or in direction, comes from having learned the preferences\.

The surprise is the shuffled\-words control\. Text with its word order scrambled, which has little to learn beyond word frequencies, gives the most concentrated update on both models: stable rank 0\.042 on Qwen and 0\.009 on SmolLM2, with 9% and 21% of the energy in a single direction\. This holds in every quarter of the network \(Table[12](https://arxiv.org/html/2610.22438#A4.T12)\)\. The model fits this data poorly \(training loss 5\.4, against 2\.2 for wikitext; Table[8](https://arxiv.org/html/2610.22438#A1.T8)\), and we do not know why that gives a more concentrated update\. One explanation we tested, that the update mainly pushes the output towards frequent tokens, does not single it out: the top directions of the SFT and code updates line up with token frequency in late layers too \(Appendix[D](https://arxiv.org/html/2610.22438#A4)\)\. We report it as an observation: the concentration of a fine\-tuning update depends on the training process and the data, not on whether the data teaches instruction following or preferences\.

### 4\.4Released models

Figure 3:Released updates \(blue\) against a Gaussian matrix of the same shape \(grey\), in three groups: base/instruct releases, the OLMo 2 post\-training stages, and code/math specialists\. Left: the threshold count \(axis starts at 0\.85\)\. Right: stable rank\.Table 3:Released pairs, means over matrices\. “Above floor” is the share of the update’s singular values larger than the largest singular value of the simulated bf16 rounding error: directions that rounding alone cannot produce \(§[2](https://arxiv.org/html/2610.22438#S2)\)\. It is not computed \(–\) for OLMo 2 base to SFT, whose base, a mid\-training checkpoint, is stored in fp32\. The last column drops the top direction, to check that one outlier does not drive the result\.Released instruct models go through much larger and more varied post\-training than our runs\. The same pattern holds for all thirteen pairs \(Figure[3](https://arxiv.org/html/2610.22438#S4.F3), Table[3](https://arxiv.org/html/2610.22438#S4.T3)\)\. The threshold count reads 91–99%, close to noise; stable rank puts every update 1\.6 to 27 times below noise, and dropping the top direction changes little, so no single outlier drives it\. Every update also has tens to hundreds of directions above the largest singular value a same\-size Gaussian matrix would have \(Table[13](https://arxiv.org/html/2610.22438#A5.T13)\)\.

For most pairs, bf16 rounding is not a concern: 91–100% of their directions are stronger than anything rounding alone can produce\. For three it is: 14% of the entries of the Qwen2\.5\-1\.5B update, and 39% and 52% of the OLMo DPO and RL updates, are exactly zero, and only 78%, 13% and 3% of their directions rise above the simulated rounding floor \(Tables[3](https://arxiv.org/html/2610.22438#S4.T3)and[13](https://arxiv.org/html/2610.22438#A5.T13)\)\. For these updates much of what the threshold count counts may be rounding\. Rounding adds many tiny singular values, which stable rank largely ignores\.

The OLMo 2 stages show where post\-training changes the weights\. Almost all of the change is in SFT: its update is 9\.8% of the size of the weights, has stable rank 0\.080 against 0\.336 for noise, and the whole base\-to\-instruct update has the same size and shape to within 0\.001\. The DPO and RL stages are tiny, under half a percent of the weights, and only 13% and 3% of their directions rise above the simulated rounding floor\. Their very low stable rank therefore reflects a few real directions on top of rounding, and we draw no conclusion about preference training from them; our own DPO runs \(§[4\.3](https://arxiv.org/html/2610.22438#S4.SS3)\) are the controlled test\.

The specialists give a mixed picture\. Against an instruct release of the same base, Qwen2\.5\-Coder\-0\.5B \(stable rank 0\.194\) is more concentrated than Qwen2\.5\-0\.5B\-Instruct \(0\.280\), while Qwen2\.5\-Math\-1\.5B and Qwen2\.5\-Coder\-1\.5B \(0\.200 and 0\.191\) are less concentrated than Qwen2\.5\-1\.5B\-Instruct \(0\.051\)\. The specialists differ from the instruct models in both content and amount of training \(their updates are about as large as the weights themselves\), so this is not a controlled comparison; our matched runs in §[4\.3](https://arxiv.org/html/2610.22438#S4.SS3)are\. What the released models show is that concentration varies with how much and what kind of training was done, and that nothing in it sets instruct updates apart\.

## 5Case study: is post\-training superficial?

[Wu et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib3)compare released base and instruct models \(Llama 3\.1 and 3\.2,[Grattafiori et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib47), and Qwen3\) through the entropy effective rank \(eRank, §[2](https://arxiv.org/html/2610.22438#S2)\) of each weight matrixWW\(not ofΔ​W\\Delta W\)\. They find it almost unchanged by post\-training, at about 85% of full rank, and read this as weight\-level evidence that post\-training is superficial\. They also propose an edit, Timber: keep the top⌈eRank⁡\(Δ​W\)⌉\\lceil\\mathrm\{eRank\}\(\\Delta W\)\\rceilsingular directions of the update and scale the rest byλ<1\\lambda<1, withλ=0\.2\\lambda=0\.2recommended, which improves Mean@kkand pass@kkon their benchmarks\. We check both with the baselines of §[2](https://arxiv.org/html/2610.22438#S2)\.

### 5\.1An unchanged effective rank is what any update of this size gives

Figure 4:Left: size of the change in the effective rank of the full weight matrixWW,\|Δ​eRank​\(W\)\|/eRank⁡\(W\)\|\\Delta\\,\\mathrm\{eRank\}\(W\)\|/\\mathrm\{eRank\}\(W\)averaged over matrices, for the real base\-to\-instruct update \(blue\) and a random update of the same Frobenius norm \(grey\)\. Right: perplexity on held\-out wikitext of Qwen3\-0\.6B base, unchanged, after a random update of the same size as its real post\-training update \(Gaussian, or with the real update’s singular values\), and after the real update, which gives the instruct model\. The numbers above the bars give the size of the change in eRank\(WW\) for each update, as in the left panel\.The measurement reproduces\. On Qwen3\-0\.6B and Qwen3\-8B, two of their pairs, the effective rank of the base weights is 0\.84 and 0\.86 of full rank, and post\-training changes it by only 0\.13% and 0\.06%\.

But a random update of the same size also leaves it almost unchanged \(Figure[4](https://arxiv.org/html/2610.22438#S5.F4), left\)\. On all seven base/instruct pairs, whose updates are 1–13% of the size of the weights, real and random updates both move the effective rank ofWWby at most 0\.5%\. The real update moves it 1\.6 to 3\.8 times less than the random one, so post\-training does changeWWin a structured way, but that is visible only next to the random comparison\.

Table 4:GSM8K accuracy, in percent \(greedy, all 1,319 test problems\), of Qwen3\-0\.6B with a random update of the same size as its real post\-training update, added to every attention and MLP matrix\. Each pair uses the same prompt and token limit: the base model an 8\-shot plain\-text prompt, the instruct model its chat template\. Differences in points with 95% paired bootstrap intervals\.An unchanged effective rank also says nothing about whether the model still works\. Adding to Qwen3\-0\.6B base a random update of the same size as its real post\-training update, matrix by matrix, moves its effective rank by 0\.5%, but its GSM8K accuracy falls from 59\.5% to 4–6%, whether the update is Gaussian or has exactly the real update’s singular values \(Table[4](https://arxiv.org/html/2610.22438#S5.T4); details in Appendix[G](https://arxiv.org/html/2610.22438#A7)\)\. The same random update added to the instruct model takes it from 64\.5% to 11\.9%\. The real update, which moves the effective rank even less \(0\.13%\), produces the instruct model\. So an update can wreck a model or turn it into a working assistant and leave the effective rank ofWWalmost the same either way\. Perplexity on wikitext rises from 18\.1 to 33\.1 with either random update \(Figure[4](https://arxiv.org/html/2610.22438#S5.F4), right\), but the real update raises it too, to 50\.1, because an instruct model no longer predicts plain web text well\. An unchanged effective rank therefore cannot tell a superficial change from a deep one, or from a destructive one\. This does not show that post\-training is deep; it shows that this measurement cannot decide the question\.

### 5\.2The edit does not need the effective\-rank cutoff

Figure 5:GSM8K pass@kkfor Qwen3\-0\.6B \(non\-thinking mode\) with tail edits and with uniform scaling of the whole update\. Eight samples per problem, the same sampling seed per problem for every variant\. Left: first 300 test problems, main variants \(every variant is in Table[15](https://arxiv.org/html/2610.22438#A8.T15)\)\. Right: all 1,319 \(Table[5](https://arxiv.org/html/2610.22438#S5.T5)\)\.Table 5:Edits of the Qwen3\-0\.6B update on all 1,319 GSM8K test problems; pass@kkin percent\. “Unscaled” is the share of the update’s energy the edit leaves at full strength \(uniform scaling shrinks every direction by the same factor\); “answered” is the share of samples with a final boxed answer; “same size” means scaled to the size of the stable\-rank edit\. Differences from the unedited model in points, with 95% paired bootstrap intervals over problems, not corrected for multiple comparisons\.Because the effective rank ofΔ​W\\Delta Wsits close to its noise value, the cutoff it gives is high: on Qwen3\-0\.6B it keeps 83% of the directions and 98\.9% of the update’s energy, so the edit touches only the last 1% \(Wu et al\. report 98\.82% for Qwen3\-8B\)\. An edit that small is also fragile in practice: running the edited model in bf16 distorts it by 16% of its size atλ=0\.2\\lambda=0\.2and 25% atλ=0\.5\\lambda=0\.5\(Appendix[H](https://arxiv.org/html/2610.22438#A8)\)\.

We compare edits of the same update on two benchmarks: GSM8K\([Cobbe et al\., 2021](https://arxiv.org/html/2610.22438#bib.bib52)\), which is not among Wu et al\.’s, and GPQA\-Diamond\([Rein et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib48)\), which is\. On GSM8K we score with pass@kk\([Chen et al\., 2021](https://arxiv.org/html/2610.22438#bib.bib53)\)and compare: Timber’s tail edit, the same edit with a stable\-rank cutoff that scales 53 times more of the update’s energy, and simply scaling the whole update by one factor per matrix \(0\.75 on average\) so that the edited update has the same size as the stable\-rank edit\. We run Timber’s edit both at its recommendedλ=0\.2\\lambda=0\.2and atλ=0\.5\\lambda=0\.5, and use Qwen3’s non\-thinking mode, the mode of Wu et al\.’s main table\.

On all 1,319 problems, Timber’s edit has no detectable effect at either setting \(Table[5](https://arxiv.org/html/2610.22438#S5.T5), Figure[5](https://arxiv.org/html/2610.22438#S5.F5)\)\. Atλ=0\.2\\lambda=0\.2pass@1 is unchanged \(−0\.0\-0\.0points;−0\.8\-0\.8,\+0\.8\+0\.8\) and pass@8 moves by\+0\.2\+0\.2\(−1\.4\-1\.4,\+1\.8\+1\.8\); atλ=0\.5\\lambda=0\.5the changes are\+0\.7\+0\.7\(−0\.0\-0\.0,\+1\.6\+1\.6\) and\+0\.8\+0\.8\(−0\.6\-0\.6,\+2\.3\+2\.3\)\. The stable\-rank edit gives a similar pass@1 and a pass@8 gain of\+1\.8\+1\.8\(\+0\.2\+0\.2,\+3\.5\+3\.5\)\.

Simply scaling the whole update does better than either tail edit: pass@1 rises by\+3\.4\+3\.4points \(\+2\.4\+2\.4,\+4\.5\+4\.5\) and pass@8 by\+2\.7\+2\.7\(\+1\.1\+1\.1,\+4\.2\+4\.2\), with nearly the same share of answered samples \(96\.4% against 97\.4%\)\. It makes the update as small as the stable\-rank edit does, but evenly from every direction instead of from the tail\. So on this benchmark the gain comes from making the update smaller, and choosing which directions to shrink by a spectral cutoff, whether eRank or stable rank, adds nothing\. Task arithmetic already treats the scale of an update as a knob worth tuning\([Ilharco et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib22)\); here that knob alone beats the spectral edits\.

Table 6:The same edits on GPQA\-Diamond\([Rein et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib48)\), Wu et al\.’s benchmark, 198 questions, non\-thinking mode with their sampling settings\. “Accuracy” is the mean over samples \(their Mean@kk\), in percent, as is pass@4; eight samples per question for the unedited model, four for each edit\. Differences in points with 95% paired bootstrap intervals over questions\.GPQA\-Diamond is where Wu et al\. report their largest gain for this model: a mean accuracy of 28\.79% against 23\.74% unedited,\+5\.1\+5\.1points\. Our unedited model scores 25\.9%, about two points above theirs\. Timber’s edit, at each of the threeλ\\lambdavalues they searched, moves accuracy by under a point, and every interval includes zero \(Table[6](https://arxiv.org/html/2610.22438#S5.T6)\)\. We do not observe their gain, but our setup is our own, not their evaluation harness: our prompt and answer format, our answer extraction, four samples per question against their three full repeats, and 2,048 new tokens against their 8,192\. Truncation, at least, does not explain the difference\. The share of samples that end without a final answer is 3\.5% for the unedited model and 3\.4–4\.2% for Timber’s three edits \(8\.7–8\.8% for the two larger edits\), so Timber’s edits are cut off no more often than no edit\. A rerun of the unedited model and the recommendedλ=0\.2\\lambda=0\.2with the limit doubled to 4,096 tokens, the most this model’s samples fit on our GPU, gives 25\.6% against 25\.4%, a difference of−0\.3\-0\.3points \(−3\.5\-3\.5,\+3\.0\+3\.0\), with 2\.7–2\.9% of samples unfinished \(Appendix[H](https://arxiv.org/html/2610.22438#A8)\)\. With 198 questions our intervals are about±3\\pm 3points, and their\+5\.1\+5\.1, from the same 198 questions, carries a similar uncertainty\. Under our settings the intervals exclude a gain of five points; a gain of one to three points is not ruled out\. Here, unlike on GSM8K, the larger edits hurt: shrinking most of the update, whether by the stable\-rank cutoff or evenly, costs 3–5 points of mean accuracy \(intervals just reaching zero\) and makes the model answer at length, while the uniform version’s pass@4 rises\. That pattern, worse single answers but more varied ones, is a change in behaviour, not a clear improvement, and with about thirty comparisons across our edit tables one interval just clearing zero is what chance would give\.

Taken together, the two benchmarks say the same thing about the cutoff\. An edit that scales only the last 1% of the update’s energy does nothing we can measure, on GSM8K or on GPQA\. Edits that scale a quarter of the update change the model’s behaviour much more, for better \(GSM8K\) or for worse \(GPQA\), and the spectral cutoff is not what decides it\.

On the first 300 problems we also ran the extremeλ=0\\lambda=0, which removes the tail completely \(Table[15](https://arxiv.org/html/2610.22438#A8.T15)\)\. Removing Timber’s tail, 1\.1% of the update’s energy, changes nothing measurable \(\+0\.5\+0\.5points of pass@1\)\. Removing the stable\-rank “tail”, which is 59% of the update’s energy and so most of the update, costs 4\.2 points against the unedited model and 5\.3 against halving it\. Removing most of an update hurts; this says little about the weakest directions alone\. A uniform scaling matched in size to Timber’s edit is almost erased by bf16 storage \(88% of the change is lost\) and, like Timber’s edit, has no clear effect \(\+0\.8\+0\.8;−0\.8\-0\.8,\+2\.4\+2\.4\)\.

We did not test thinking mode, where Wu et al\. also report gains, and our GPQA intervals are wide\. Within those limits, the effective\-rank cutoff is not what makes an edit of this kind work\.

## 6Related work

##### Noise baselines for spectra\.

Comparing a spectrum against what noise would give is old\. Parallel analysis\([Horn, 1965](https://arxiv.org/html/2610.22438#bib.bib31)\)keeps only the factors whose eigenvalues beat those of random data, and[Gavish and Donoho \(2014\)](https://arxiv.org/html/2610.22438#bib.bib32)derive the optimal threshold for separating signal singular values from Gaussian noise\. Random matrix theory has also been used to study trained weight matrices: their spectra depart from those of random matrices in heavy\-tailed ways that track training quality\([Martin and Mahoney, 2021](https://arxiv.org/html/2610.22438#bib.bib33)\), while much of the bulk still follows random\-matrix statistics\([Thamm et al\., 2022](https://arxiv.org/html/2610.22438#bib.bib34)\)\.[Staats et al\. \(2023\)](https://arxiv.org/html/2610.22438#bib.bib35)use those statistics to separate the noise part of a weight matrix from its information, and[Hartford et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib36)use them to choose which layers to train\. For fine\-tuning,[Biderman et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib12)compared the spectrum of a fully fine\-tuned weight matrix with that of the pretrained matrix plus Gaussian noise and found them alike\. We compare the update itself with noise, measure by measure, and find that the answer depends on which measure one uses\.

##### Superficial alignment\.

[Zhou et al\. \(2023\)](https://arxiv.org/html/2610.22438#bib.bib1)proposed that alignment mostly selects a format the pretrained model already supports, and[Lin et al\. \(2024\)](https://arxiv.org/html/2610.22438#bib.bib2)found that base and aligned models differ mainly on stylistic tokens\. Others have questioned how far this goes: safety behaviour can be confined to the first few output tokens\([Qi et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib4)\), and post\-training keeps improving reasoning with more data\([Raghavendra et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib5)\)\.[Wu et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib3)looked for weight\-level evidence through the effective rank of released models \(§[5](https://arxiv.org/html/2610.22438#S5)\)\.[Chaudhury \(2025\)](https://arxiv.org/html/2610.22438#bib.bib6)locates the effect of preference tuning in a few middle layers by activation patching, a question about activations that our weight analysis does not address\.

##### The rank of fine\-tuning updates\.

Fine\-tuning can be carried out in a small random subspace\([Aghajanyan et al\., 2021](https://arxiv.org/html/2610.22438#bib.bib10)\), the idea behind LoRA\([Hu et al\., 2022](https://arxiv.org/html/2610.22438#bib.bib11)\), and fine\-tuned models can be stored as low\-rank approximations of the update;[Ryu et al\. \(2023\)](https://arxiv.org/html/2610.22438#bib.bib16)also plot the singular values of an update against a Marchenko–Pastur reference and find them more concentrated\.[Zhang et al\. \(2023\)](https://arxiv.org/html/2610.22438#bib.bib17)find that fine\-tuning moves the weights within a small task\-specific subspace\. Measured directly, full fine\-tuning updates need a rank 10–100 times larger than typical LoRA ranks to hold 90% of their energy\([Biderman et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib12)\), and reinforcement\-learning and preference\-tuning updates are reported as nearly full rank, 99\.2–99\.8% of the maximum\([Mukherjee et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib19)\)\. Both statements count directions; our results agree with them and add that the same updates are far more concentrated than noise at the top of the spectrum\.[Shuttleworth et al\. \(2025\)](https://arxiv.org/html/2610.22438#bib.bib14)compare singular vectors of fine\-tuned and pretrainedWWand find that LoRA introduces new dominant directions that full fine\-tuning does not\. Delta\-CoMe\([Ping et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib15)\)observes that update spectra are long\-tailed and compresses them by giving more bits to the top singular vectors, finding that plain low\-rank truncation hurts; BitDelta\([Liu et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib26)\)goes further and keeps only the sign of each entry of the update plus one scale per matrix, with little loss\.[Paul \(2026\)](https://arxiv.org/html/2610.22438#bib.bib18)uses stable rank among other features of LoRA updates to tell training objectives apart\.

##### Editing updates\.

Updates can be added, scaled and merged\([Ilharco et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib22)\), and much of an update can be dropped or trimmed at random or by magnitude before merging with little loss\([Yu et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib27);[Yadav et al\., 2023](https://arxiv.org/html/2610.22438#bib.bib23)\)\. Scaling an update as a whole is an old and effective edit: interpolating between pretrained and fine\-tuned weights makes fine\-tuning more robust\([Wortsman et al\., 2022](https://arxiv.org/html/2610.22438#bib.bib24)\), and extrapolating along the alignment update can improve an aligned model\([Zheng et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib25)\)\. Timber’s tail edit belongs to this family, and our comparison with uniform scaling \(§[5\.2](https://arxiv.org/html/2610.22438#S5.SS2)\) asks whether its spectral cutoff adds anything over the simplest edit of this kind\.

##### Low precision\.

Rounding weights to bf16 cancels small updates\([Zamirai et al\., 2020](https://arxiv.org/html/2610.22438#bib.bib28)\), and in reinforcement learning this can make updates look sparse\([Zhu et al\., 2025](https://arxiv.org/html/2610.22438#bib.bib20)\)\. We found the same effect in our own first runs \(§[3](https://arxiv.org/html/2610.22438#S3)\) and show that it can also inflate the threshold count of released checkpoints with small updates \(§[4\.4](https://arxiv.org/html/2610.22438#S4.SS4)\)\.

##### Why updates concentrate\.

Gradient descent spends most of its motion in a small subspace\([Gur\-Ari et al\., 2018](https://arxiv.org/html/2610.22438#bib.bib21)\), and gradients of linear layers are approximately low rank\([Zhao et al\., 2024](https://arxiv.org/html/2610.22438#bib.bib13)\), so a sum of gradient steps can inherit a few dominant directions\. We do not test this mechanism\.

## 7Discussion

##### What the measures are good for\.

None of the five measures is wrong; they answer different questions\. Counting measures say how many directions an update touches, and for fine\-tuning the answer is “almost all”\. Stable rank and the participation ratio say how unevenly the energy is spread, and the answer is “very”\. We do not recommend stable rank over the others: it depends on a single direction, it is also far below noise for the pretrained weights and for the difference of two unrelated checkpoints, not only for a real update, and a cutoff built on it edited a model no better than one built on eRank\. The mistake is to read any one of these numbers without the value for noise next to it, or to take a property of all fine\-tuning as evidence about alignment\.

##### Check where a checkpoint comes from\.

The obvious base for the OLMo 2 1B SFT checkpoint, the main revision of the released base model, is not its parent: the two share no initialisation, and the real parent is the final mid\-training checkpoint, published only as a branch \(§[3](https://arxiv.org/html/2610.22438#S3)\)\. The difference between the unrelated pair still has a plausible\-looking spectrum, with stable rank 4\.4 times below noise, much like the real update\. Nothing in a rank measure flags such a mistake; a cosine between the two sets of weights does, and costs nothing\.

##### Limitations\.

- •One model for preference training\.The DPO runs and their swapped control are on Qwen2\.5\-0\.5B only\. Reinforcement learning appears only in the released OLMo 2 stage, which is too small to measure above rounding\.
- •Scale of our own training\.Our fine\-tunes are 0\.36B and 0\.5B parameters with about two million tokens per epoch\. The measurement results hold on released models up to 8B, but we do not study training at that scale\.
- •Tokens or steps\.Matching the training tokens leaves the code runs with 2\.6–2\.7 times fewer optimizer steps than SFT; matching the steps gives them 2\.5–2\.7 times more tokens\. No single control matches both, and the two give different code updates\.
- •Which null\.A Gaussian matrix is the least structured baseline possible, and even the difference of two unrelated trained checkpoints beats it\. We add the pretrained weights as a harder reference, and matched fine\-tunes without alignment content as the real test, but other baselines \(for instance updates from other optimizers\) could tell more\.
- •Seeds\.The SFT, wikitext, code and DPO runs were repeated once; the shuffled\-words and step\-matched runs were not\. Two seeds bound the run\-to\-run variation only roughly\.
- •Released models are black boxes\.Apart from OLMo 2, their data and recipes differ in many ways at once, so they test the measurement, not any claim about alignment\.
- •Loss masking differs\.SFT computes the loss on answer tokens only, the controls on every token; the tokens seen are matched, the tokens trained on are not\.
- •The shuffled\-words result is unexplained\.The one explanation we tested, alignment with token frequency, is shared by other runs\.
- •Directions, measured coarsely\.The overlap of top\-16 subspaces shows that the data steers the directions of an update; it does not say which directions, or what they do\.
- •The edit experiment is narrow:one model, non\-thinking mode only, and 198 GPQA questions, which leaves intervals of about±3\\pm 3points\.
- •One random\-update test\.The damage test uses one model, Qwen3\-0\.6B, and one task, GSM8K\.

## 8Conclusion

Rank measures that count directions describe fine\-tuning updates as nearly full rank and put them only a little below random matrices of the same shape\. Measures that weigh the top directions show the same updates to be far more concentrated than noise, and more concentrated than the pretrained weights\. Both are right: the updates have a few strong directions and a long tail that holds most of the energy\. With the amount of training held fixed, the data shapes an update somewhat, but instruction tuning does not stand out from Wikipedia or code; DPO gives the same shape and directions with real or half\-swapped preferences; and scrambled text gives the most concentrated update\. The shape is a property of fine\-tuning, not a mark of alignment\. An unchanged effective rank of the weights after post\-training is what a random update of the same size also produces, and an edit built on the effective rank of the update does nothing measurable on two benchmarks\. Our recommendation is simple: report any rank measure of a weight update next to its value on a random matrix of the same shape, check that low\-precision training or storage did not erase the update, check that the two checkpoints are really related, and test claims about alignment against a fine\-tune without alignment content\.

#### Broader Impact Statement

This paper is about measurement methodology for analysing fine\-tuned language models; it introduces no new capabilities or training methods\. Its main practical consequence is caution about reading weight\-space statistics as evidence that alignment is shallow or deep, since such claims can affect how much trust is placed in alignment training\.

#### Reproducibility

Every run records its configuration, its exact training rows, its seed, its token count and the fraction of weights left unchanged\. We will release the code, the configurations and run manifests, the saved singular\-value spectra of every update, the random\-update seeds, the edit scripts and the evaluation prompts; they are withheld while the paper is under review\.

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## Appendix

## Appendix ATraining details

Table 7:Settings shared by all our fine\-tunes\. Each language\-model run trains on the same number of tokens as the SFT run of the same model, counted after truncation\. DPO uses the same precision, memory settings and batch, with the changes listed at the bottom\.Table 8:Every fine\-tune\. Steps are optimizer steps \(rounded to 10\); loss is the mean training loss;‖Δ​W‖F\\\|\\Delta W\\\|\_\{F\}is over all attention and MLP matrices\. The second SFT seed was interrupted and resumed from step 1,600 with its optimizer and scheduler state, so its logged mean loss covers only the last steps and is not shown\.Training a run took 1\.3–3\.7 hours on one GPU, and 3\.6–8\.6 hours for DPO \(Table[8](https://arxiv.org/html/2610.22438#A1.T8)\)\. Held\-out reward accuracy, on about 190 validation pairs that are never swapped, is 65% and 74% for the two DPO seeds and 51% for the swapped control\. The base tokenizer of SmolLM2\-360M has no chat template, so SFT borrows the one from SmolLM2\-360M\-Instruct\. Second seeds change both the training seed and the data sample\. Every run records its exact training rows, token count and the fraction of unchanged weights\. Dropping the top direction leaves every update far below noise, whose stable rank without its own top direction is 0\.440 for Qwen and 0\.357 for SmolLM2, so stable rank is not driven by a single outlying direction\.

## Appendix BThreshold sensitivity and the noise baseline

Table 9:The threshold count at three cutoffs\. At0\.01​σ10\.01\\,\\sigma\_\{1\}every update looks almost like noise; at0\.1​σ10\.1\\,\\sigma\_\{1\}the gap is large\. The verdict depends on an arbitrary choice\.Table 10:Stable rank of the random\-init pair against the predictionm​n/\(m\+n\)2/rmn/\(\\sqrt\{m\}\+\\sqrt\{n\}\)^\{2\}/rfor a Gaussian matrix of the same shape, Qwen2\.5\-0\.5B, mean over layers\.Figure 6:How far below noise each update is,1−Rα​\(update\)/Rα​\(noise\)1\-R\_\{\\alpha\}\(\\text\{update\}\)/R\_\{\\alpha\}\(\\text\{noise\}\)as means over matrices, along the Rényi family fromα=1/4\\alpha=1/4toα=∞\\alpha=\\infty\(stable rank, squares\)\. The gap grows with the order and levels off from aboutα=8\\alpha=8\.
## Appendix CStable rank by matrix type

Table 11:Stable rank \(fraction of maximum rank\) by matrix type\.Every matrix type of every update is far below noise in both models\. Within a model the SFT, wikitext and code updates are close in every column, and the shuffled\-words update is the most concentrated in every column\. On SmolLM2 every type of every update is also below the pretrained weights\.

## Appendix DThe shuffled\-words update

Table 12:Stable rank by quarter of the network\.We tested one possible explanation: that the shuffled\-words update mainly shifts the output towards frequent tokens\. For each layer’sdownprojection update on Qwen, we map the top left singular vector to the vocabulary through the final norm and the tied unembedding \(ignoring the layers in between, as the logit lens does\) and correlate the resulting logit shift with the log frequency of each token in the run’s training data, against 50 random directions\. In the last third of the network the top direction of several runs lines up with frequency, not only shuffled words: the correlation beats the random 95th percentile \(about 0\.19\) in layers 18–23 for shuffled words, in most of layers 15–23 for SFT and code, and in layer 23 for wikitext\. The mean correlation over the last third is 0\.33 for shuffled words, 0\.25 for SFT, 0\.19 for code and 0\.09 for wikitext\. With 24 layers and four runs, and no correction for multiple tests, we read this only as a pattern: frequency alignment in late layers is common to fine\-tuning, so it does not explain why the shuffled\-words update is the most concentrated\.

## Appendix EReleased pairs: more measures

Table 13:More on the released pairs\. “Particip\. ratio”: the participation ratio, next to its value for a Gaussian matrix of the same shape\. “Above edge”: the number of singular values above the largest one such a Gaussian matrix would have \(mean per matrix\)\. “Rounding share”: the number of singular values of the simulated bf16 rounding error above0\.01​σ10\.01\\,\\sigma\_\{1\}of the update, as a share of the update’s threshold count; a loose upper bound on how much of the count rounding could explain, as a ratio of means over matrices \(compare the “above floor” column of Table[3](https://arxiv.org/html/2610.22438#S4.T3)\)\.‖Δ​W‖F/‖W‖F\\\|\\Delta W\\\|\_\{F\}/\\\|W\\\|\_\{F\}: the size of the update relative to the base weights\. “Zero entries”: the share of entries ofΔ​W\\Delta Wthat are exactly zero, the direct trace of rounding\.Qwen2\.5\-0\.5B is the least concentrated instruct release on every rank measure \(not on top\-1 energy\), and less concentrated than our own SFT of the same base; we do not know why\.

The two direct checks agree\. Where few directions rise above the rounding floor, many entries of the update are exactly zero: 14% for Qwen2\.5\-1\.5B, and 39% and 52% for the OLMo DPO and RL stages, whose updates are under half a percent of the weights\. For the other instruct releases 1\.5–3\.1% of entries are zero and 91–99% of directions are above the floor\. The rounding share is much higher for several of these pairs \(for instance 76% for Qwen2\.5\-0\.5B\), which shows how loose a bound it is: it compares rounding with0\.01​σ10\.01\\,\\sigma\_\{1\}, not with the directions the update actually has\. For the specialists, whose updates are as large as the weights themselves, almost no entry is zero\.

## Appendix FDirection overlap between updates

For each matrix we take the top\-16 left singular vectors of each of two updates,UAU\_\{A\}andUBU\_\{B\}, and compute‖UA⊤​UB‖F2/16\\\|U\_\{A\}^\{\\top\}U\_\{B\}\\\|\_\{F\}^\{2\}/16, which is 1 when the two subspaces coincide and16/m16/mfor two random 16\-dimensional subspaces ofℝm\\mathbb\{R\}^\{m\}\. We report the mean over matrices with a layer\-bootstrap interval \(Table[14](https://arxiv.org/html/2610.22438#A6.T14)\)\. Right singular vectors give the same ordering, with smaller overlaps between runs on different data\.

Table 14:Overlap of the top\-16 left singular subspaces of two updates, mean over matrices, with 95% layer\-bootstrap intervals\.Two things stand out\. The data moves the directions more than it moves the shape: on SmolLM2 the overlap between runs on different data \(0\.12–0\.13\) is a quarter of the overlap between seeds of the same run \(0\.34–0\.51\), while their stable ranks differ by at most 0\.014\. And wikitext and shuffled words, which share their words, overlap more than wikitext and code do\.

## Appendix GRandom\-update details

Each random update is drawn matrix by matrix with its own seed and scaled to the Frobenius norm of the real update of that matrix; embeddings and norms are left alone\. The edit is made in fp32 and the model then runs in bf16\. Answers are greedy, up to 256 new tokens for the base model \(8\-shot prompt from the first eight GSM8K training problems, answer after “The answer is”\) and 512 for the instruct model \(chat template, thinking off, answer in`\\boxed\{\}`\)\. Many answers from the randomly updated base models hit the token limit \(29–59%, against 5% for the unedited base\), but even the ones that finish are right only 7–8% of the time, against 63% for the base model\. The instruct model with a random update hits its 512\-token limit on 72% of problems; on the rest it is right 28% of the time, against 66% for the unedited instruct model\. Part of its drop to 11\.9% is therefore rambling rather than wrong answers, but the finished answers show the damage too\.

We also scored the base model plus its real update with the base model’s 8\-shot prompt\. It reaches only 19\.9%\. That is not clear evidence of damage: post\-trained weights write long chat\-style reasoning in that format, and 59% of their answers hit the 256\-token limit, about as many as with the first Gaussian update\. What separates them is the answers that finish: 42% are right with the real update, 7–8% with the random ones\. This combination also keeps the base model’s embeddings, which post\-training changed by 13%\. The fair test of the real update is the instruct model in its own format \(Table[4](https://arxiv.org/html/2610.22438#S5.T4)\)\.

## Appendix HEdit experiment details

On GPQA\-Diamond the prompt gives the question and its four options, shuffled once per question with a fixed seed, and asks for “Answer: $LETTER” as the last line; the answer is the last such line \(or the last`\\boxed\{\}`letter\)\. We use Wu et al\.’s sampling settings for this mode \(temperature 0\.7, top\-pp0\.8, top\-kk20\), with up to 2,048 new tokens where they allow 8,192, eight samples per question for the unedited model and four for each edit where they run three full repeats; pass@4 is the unbiased estimate from those samples\. The share of samples that reach the limit without a final answer is 3\.5% unedited, 3\.8%, 4\.2% and 3\.4% for Timber’s edit atλ=0\.2\\lambda=0\.2,0\.50\.5and0\.80\.8, and 8\.8% and 8\.7% for the stable\-rank cutoff and uniform scaling, which make the model answer at length\.

To check that the limit is not hiding a gain, we reran the unedited model and theλ=0\.2\\lambda=0\.2edit with 4,096 new tokens, four samples per question for both\. Wu et al\.’s 8,192 does not fit on our 6 GB GPU with four samples at once, because on a few questions this model writes very long answers\. We began the unedited model at that limit with samples generated one at a time, ran the first 111 questions that way, then lowered the limit to 4,096; all 111 finished well within either limit\. At the longer limit the unedited model scores 25\.6% \(pass@4 44\.9\) and the edit 25\.4% \(pass@4 47\.5\), differences of−0\.3\-0\.3\(−3\.5\-3\.5,\+3\.0\+3\.0\) and\+2\.5\+2\.5\(−3\.5\-3\.5,\+8\.6\+8\.6\) points, and 2\.9% and 2\.7% of samples are unfinished\. Doubling the limit changes neither model’s score by more than a point\.

On GSM8K the prompt is the question followed by “Please reason step by step, and put your final answer within`\\boxed\{\}`\.”, in Qwen3’s chat template with thinking turned off, sampled at temperature 0\.7, top\-pp0\.8 and top\-kk20 for up to 512 new tokens\. The answer is the last`\\boxed\{\}`expression, or the last number if there is none\. The edit is applied to every attention and MLP projection in fp32 and the model then runs in bf16\. Rounding then distorts the edit: the error‖bf16⁡\(W′\)−W′‖F\\\|\\mathrm\{bf16\}\(W^\{\\prime\}\)\-W^\{\\prime\}\\\|\_\{F\}, whereW′W^\{\\prime\}is the edited matrix, is on average 25% \(16% atλ=0\.2\\lambda=0\.2\) of the intended change‖W′−W‖F\\\|W^\{\\prime\}\-W\\\|\_\{F\}for Timber’s tail edit, 4% for the stable\-rank tail edit, 5\.5% for uniform scaling matched to the stable\-rank edit and 88% for uniform scaling matched to Timber’s edit, which bf16 storage almost erases\. The uniform scaling factor is computed per matrix; its mean is 0\.75 for the stable\-rank match\. The pass@kkvalues use the unbiased estimator of[Chen et al\. \(2021\)](https://arxiv.org/html/2610.22438#bib.bib53)withn=8n=8\.

Table 15:All edit variants on the first 300 GSM8K test problems, pass@kkin percent\. Differences from the unedited model in points, with 95% paired bootstrap intervals, not corrected for the fourteen comparisons\. “Answered” is the share of samples with a final boxed answer\. “Uniform” scales the whole update, per matrix, to the size of the named tail edit\.