Is Newborn Wiring Special? Separating Wiring from Weight Placement in Connectome Reservoirs

Publication

NeurIPS 2026 DevAI workshop

Abstract

Reservoir computing offers a way to study the brain’s wiring before it is even trained. The recurrent network remains fixed, while only a linear readout is trained. The human connectome is found to perform better than randomly rewired versions of itself, suggesting that biological wiring is special. To understand the source of this advantage, a mathematical graph-theoretic decomposition is introduced. Rewiring a weighted network changes both the regions that are connected and the weights assigned to those connections. The observed advantage therefore combines an effect of wiring with an effect of weight placement.

These effects are separated by averaging the wiring term over the null model’s weight rule, as a single draw introduces about one $z$-unit of noise. Adult and infant connectomes are then considered separately. In adult Human Connectome Project graphs, weight placement explains most of the reported effect, leaving a small but consistent wiring effect. Across the full dHCP release, a large wiring effect is found at every measured gestational age at birth, while gestational age explains almost none of its variance. The connectomes are also compared with non-brain networks. A Watts–Strogatz graph matched in size, edge count, weights, and strength performs as well as or better than the connectome. The newborn connectome’s advantage is therefore real across all measured gestational ages, but it is not unique to the brain. The same separation can be applied whenever a weighted network is compared with rewired nulls.

1 Introduction

How much of a competent system is in place before learning begins? Developmental science shows that infants are born with core systems of knowledge [1], and the genomic-bottleneck argument holds that most animal behaviour appears too soon after birth to have been learned, so it must be shaped by a genome-encoded wiring [2]. We test this question using Echo State Networks (ESNs), where a recurrent reservoir is fixed and only its linear readout is trained [7, 8], so any performance difference between two reservoirs must come from structure that was never learned. In humans, the closest example of structure that precedes learning is the newborn connectome, which is already organised [35, 37]. We focus on whether a fixed reservoir actually benefits from that organisation, and whether the benefit is specific to brains or shared by a wider class of graphs.

Prior work substitutes a human structural connectome for the reservoir [10, 11, 13], and rests on one control: does the empirical graph beat a degree-preserving rewiring of itself? That control is used to isolate the wiring, and it cannot. Maslov-Sneppen rewiring [22] randomises which node pairs are joined; as applied to weighted connectomes it comes paired with a rule that reassigns the weight multiset, so it also randomises which edge carries which weight [23, 25]. The reported statistic is therefore the sum of a wiring effect and a weight-placement effect. Applied to 200 adult connectomes, the correction shrinks the reported effect by a share that depends on the null; what is left is small but significant in most subjects.

An adult-versus-neonate contrast confounds age with atlas, tractography and thresholding, so we measure the wiring term within one cohort and one pipeline: the whole dHCP structural release, 524 infants spanning 23.0-42.3 weeks of gestational age at birth.

Contributions and scope

We measure what a fixed recurrent substrate gains from a wiring diagram it never learned, and what a rewired-null comparison can establish about it. We summarize our contributions as follows:

• We derive an exact decomposition of the reported statistic: the $z$ of a graph against a rewired null ensemble is a wiring term plus a weight-placement term, and the wiring term must be averaged over the null’s weight rule (Proposition 1).
• We apply it to 200 adult Human Connectome Project graphs under the three null families in use: weight placement carries 28% to 75% of the reported effect, and what survives is small but consistent (Sections 3.3 and 4.1).
• We measure the corrected term across the whole dHCP release, 524 infants born at 23.0-42.3 weeks through one pipeline: it is large at every age, and gestational age explains under 2% of its variance (Section 4.2).
• We add the control that prior connectome-reservoir work lacks: matched non-brain graphs under the same nulls, and a direct manipulation of small-worldness (Section 4.3).

2 Related work

Suárez et al. [10] introduced the paradigm: a human connectome beats 1,000 rewirings on memory capacity at criticality, while the rewirings win in the stable and chaotic regimes unless wiring cost is charged. The conn2res toolbox [11] extends this with a 500-draw degree- and density-preserving null and proposes using connectomes “obtained throughout the lifespan” to study “computational capacity across ontogeny and phylogeny”. Mijalkov et al. [12] already focus on ageing, regressing raw capacity on age over 636 connectomes aged 18-88 through one pipeline, with no correction applied; we add the ontogenetic end and the correction. Damicelli et al. [13] compare human, macaque and marmoset connectomes against wiring-preserving and wiring-destroying surrogates, concluding that biologically inspired networks “perform as well as classical echo state networks, provided a minimum level of randomness and diversity of connections is allowed”. Nguyen et al. [14] embed fMRI-derived sub-circuits against five null families. Our results are consistent with all of these once Proposition 1 is applied. Damicelli et al.’s degeneracy does not need it: their weight rule is already matched and averaged, and is independent supporting evidence (Appendix C).

Null models work by preserving some properties of a network while randomising others [23]; which properties fall on which side is what a null model tests. Ansmann and Lehnertz [20, 21] made the weighted case explicit for brain networks, constructing surrogates that preserve edge weights or vertex strengths so that the weight collection’s influence could be “effectively segregated” from the topological characteristic under test. We apply that programme to a reservoir score. Maslov-Sneppen rewiring [22] is the workhorse; Rubinov and Sporns [24] rank-match weights to endpoint strength to preserve strength as well, a procedure built for signed functional networks and adapted, here as elsewhere, to positive structural ones. Benchmarking it against simulated annealing over 10,000 nulls per network, Milisav et al. [25] find annealing recovers the empirical strength sequence better on every dataset, and that “the choice of network null model can yield fundamentally different inferences about hitherto established phenomena”.

That graph structure per se shapes reservoir computation is established without brain data: an optimal modularity for memory [27], small-world topology stabilising the echo state property [28], modularity and link density predicting performance across 45 connectomes [29], and hierarchical-modular graphs outperforming modular and random ones [26]. Structure alone also carries competence in weight-agnostic networks, which solve control and vision tasks with a single shared weight, locating the ability entirely in the architecture [4]. The genomic-bottleneck argument asks how much of a competent network a compact code can specify [2, 3], and reservoir computing is the cleanest tool to test it [5, 6].

The structure our developmental claim rests on is already present by 30 weeks of gestation, when rich-club organisation appears [35]. The preterm period establishes the network scheme the adult brain retains [37], and prematurity leaves measurable alterations in it [36]. The dHCP release measured here [34] supports predicting age and clinical risk from the connectome alone [33]. We are not aware of any prior work that uses neonatal connectomes as reservoirs, or that asks whether a fixed dynamical substrate can use the structure they contain.

Manipulating weight placement on fixed wiring appears in several studies [13-16, 25]; outside reservoir computing the surrogate is called coordinate-preserving weight reshuffling [18, 19]. Costi et al. report that shuffling weights on the fixed Drosophila topology is statistically equivalent to randomising the topology [17]. No reported $z$ in the studies is $\delta_\omega$-corrected, and where the comparison is a $z$ against a rewired ensemble the matched side must also be averaged over the weight rule; several contrasts already average [13, 17], but none reports such a $z$. We add the identity that supplies both and the developmental gradient measured with it in one cohort and pipeline.

3 Methods

3.1 Reservoir, data and protocol

At each step the state $x(t) \in \mathbb{R}^N$ evolves as a leaky integrator:

with $\alpha$ a vector of per-neuron leak rates [9]. The readout is $y(t) = W_{\mathrm{out}}\,[1; u(t); x(t)]$, fitted by ridge regression on post-washout states. Every recurrent matrix is rescaled to a common target spectral radius, $W = \rho A / \lambda_{\max}(A)$.

Adult graphs are the 83-region Lausanne parcellation from braingraph.org [31] built on HCP diffusion imaging [32], weighted by streamline count. Neonatal graphs are the released 90-region dHCP matrices of [33, 34], thresholded to their 940 strongest edges, which is near the adult mean density: five term-born and five very preterm (< 32 weeks gestational age) for the battery, and the whole 524-infant release for Section 4.2, where the threshold is 953.

We report NARMA-10 nonlinear system identification, scored by NRMSE, throughout, and use a linear memory score $\mathrm{MC}_{\mathrm{lin}}$ only as a check; its per-delay flooring makes it a relative score (Appendix A).

Temporal tasks run at $\rho_W = 0.95$, leak range $[0.85, 1.0]$, input scale 0.1, washout 100, 2000 samples, readout ridge $10^{-6}$ (swept in Appendix B); every score is a mean over 5 reservoir seeds × 3 input draws. Null ensembles are 200 draws per family per graph, except in the 524-subject sweep, where they are 100.

Because $\omega(A)$ is a random quantity for the stochastic weight rules, we estimate $s(\omega(A))$ as a mean over $K$ independent draws and report its Monte-Carlo standard error in $z$ units with every wiring-term estimate: $K = 50$ in the battery and the synthetic ensembles, 25 in the 524-subject sweep, 30 in the Watts-Strogatz sweep. The residual MC error is $\le 0.07$ in Table 1 and up to 0.45 per subject in the 524-subject sweep, where it accounts for part of the between-subject scatter.

The two comparisons need two different tests: the naive one puts a fixed graph against an ensemble (two-sided $(k+1)/(n+1)$ permutation estimate, floor 0.005 at $n = 200$), the wiring one puts two samples against each other ($K$ weight-rule draws against $n$ nulls, two-sample permutation test over 20,000 label permutations). Across subjects we lead with the mean per-subject $z$, its SD and a one-sample $t$-test, a random-effects summary that makes between-subject variance visible. Exchangeability holds for the degree-preserving family and fails for the annealed one, whose per-subject significance counts are optimistic and never carry a conclusion alone; that, Stouffer’s $z$, and the Benjamini-Hochberg control over the battery’s 36 tests are in Appendix A.

3.2 What a null model measures

Let $s(\cdot)$ be a score on a weighted adjacency matrix. A null family $\mathcal{N} = (R, \omega)$ is a rewiring $R$ of the binary topology together with a weight rule $\omega$ that places the original weight multiset onto the rewired edges. Write $\mu$ and $\sigma$ for the mean and standard deviation of $s$ over an ensemble drawn from $\mathcal{N}(A)$, and let $\omega(A)$ denote $A$’s own wiring carrying the weight rule $\omega$. Figure 3 in Appendix A draws this in one picture.

Proposition 1 (Wiring / weight-placement decomposition). For any graph $A$ and any null family $\mathcal{N} = (R, \omega)$, writing $\bar{s}_\omega(A) = \mathbb{E}_\omega\bigl[s(\omega(A))\bigr]$ for the expectation over the weight rule,

Proof. Add and subtract $\bar{s}_\omega(A)$ in the numerator of $z_{\mathrm{naive}} = (s(A) - \mu)/\sigma$.

The expectation over the weight rule is essential. For a stochastic $\omega$ the identity holds pathwise for any single draw, but $z_{\mathrm{wiring}}$ then inherits that draw’s variance, which we measure at $\approx 1$ $z$ unit here, comparable to $\sigma$ itself and large enough to flip the sign of the wiring term for some subjects across seeds. Reading a wiring term off one draw is reading noise; we estimate $\bar{s}_\omega$ over $K \ge 25$ draws everywhere.

A null model is a test of exactly those properties it randomises while holding the rest fixed [23]; $\mathcal{N}$ is therefore a test of wiring only when $\delta_\omega = 0$. The degree-preserving, rank-matched and annealed nulls used in connectome-reservoir work all fail that condition; Damicelli et al.’s uniform-weight surrogates [13] satisfy it, at the cost of the empirical weight multiset. Every reported number is $z_{\mathrm{naive}}$; the quantity intended is $z_{\mathrm{wiring}}$. Both terms share one null ensemble, so (1) closes by construction; what needs verifying is that the matched side carries the null’s weight rule on the original wiring.

A second identity explains why one popular null misbehaves. Rescaling pins the leading eigenvalue only:

is free to vary. A null that concentrates weight onto hub-hub edges raises $\lambda_{\max}(A)$ relative to $\lVert A \rVert_F$ and so lowers the effective gain of the rescaled reservoir, which costs performance for reasons unrelated to topology.

3.3 Three null models, and what they actually preserve

We compare three families.

• Degree-preserving: Maslov-Sneppen rewiring with the weight multiset shuffled onto the result.
• Rank-matched: the same rewiring, then sorted weights assigned to edges ranked by the product of original endpoint strengths, in one pass. This is the static-sort form of the Rubinov-Sporns idea [24] that recent connectome-reservoir work adopts as its stricter control; note that it is not the procedure Rubinov and Sporns describe, which is iterative and stochastic.
• Annealed: the same rewiring, then a simulated-annealing weight assignment minimising

over permutations $\pi$ of the weight multiset onto the edges of the rewired weighted adjacency $B(\pi)$, following [25]. This preserves the degree sequence and the weight multiset exactly and the strength sequence to $r \ge 0.9958$, at about 0.3 s per null on an 83-node graph.

Measured over five adult subjects and 25 draws each, the rank-matched null pins the weight-strength coupling at 0.987 where real connectomes sit at 0.437, and recovers strength to only 0.8758, worse preservation than the annealed null (0.9998) on the very property it is named for. No rule reproduces the empirical coupling; the rank-matched one is singled out because it misses by so much more, and consistent with (2), rescaling strips most of its gain where the annealed null tracks the real graph closely (Appendix C). Its $\delta_\omega$, measured on unchanged wiring and so pure weight placement, is +0.067 NRMSE, against +0.005 degree-preserving and +0.017 annealed. In $z$ units these account for 79%, 40% and 77% of the naive adult effect each null reports (Table 1).

All of that describes the static sort. Rubinov and Sporns’ actual procedure, which recomputes expected weights from residual strengths after every placement, recovers strength to 0.9916 and returns +3.42 naive; read through it, the weight-placement share is the largest we measure anywhere, 96% (Appendix C). The inflated rank-matched column of Table 1 is a property of the shortcut alone, and the range quoted below is bounded by the nulls in current use.

4 Results

4.1 Adults

Across 200 adult connectomes, weight placement accounts for 28% of the reported degree-preserving effect, which falls from +0.98 to +0.70, and for 56% and 75% of the annealed and rank-matched ones. Table 1 applies the decomposition to the five-subject battery, and Figure 4 in Appendix A shows it per subject. Those five are not representative: their naive degree-preserving effect is +1.78 against $+0.98 \pm 0.88$ over 200 graphs drawn evenly from the 1,064 braingraph.org publishes, only 25/200 of those are individually significant, and the battery overstates all three shares. Every adult NARMA-10 share and wiring term below uses the 200 graphs.

Table 1: NARMA-10 on the five 83-node adult, five term-born and five very preterm 90-node graphs in the battery (text claims use 200 adults); $n = 200$ nulls per family, $K = 50$ draws, Monte-Carlo error $\le 0.07$. Cells are the mean per-subject $z$, bracketing how many of the five are individually significant at 0.05; the rank-matched rule is the deterministic static sort (Section 3.3), so its $K = 1$ and its brackets are not comparable with the other rows. The adult and neonatal rows are not directly comparable: the cohorts differ in atlas, tractography and thresholding (Section 3.1).

The residual adult wiring term is $+0.70 \pm 0.43$, individually significant in 157/200 graphs and at $p = 4.4 \times 10^{-59}$ against zero by a one-sample $t$-test (+1.31 and +2.63 for the other two families on the same graphs). The effect is smaller than the naive statistic reports but significant in more graphs, because the wiring test has $K$ draws on the real side: the count measures resolvability, not a larger effect. The cost of not averaging is visible in the stored scores: individual draws put the five-graph cohort mean anywhere in [+0.01, +2.07], and per subject the penalty is larger still (Appendix C).

$\mathrm{MC}_{\mathrm{lin}}$ shows the confound running the other way, reversing an apparent adult memory deficit (−2.76) into +0.30 once the weight rule is matched (Table 2).

The neonatal rows of Table 1 behave differently: the surviving wiring term is about twice the adult one against the degree-preserving null and several times it against the annealed, and against the annealed null almost none of the naive effect is weight placement (3% term-born, against 56% in adults; Appendix A). That is a property of the null family: the rank-matched one puts the neonatal shares at 72% and 79%, as confound-heavy as the adult one, so the cohort is not what changed. We do not read the adult-neonate difference as developmental, because no null model repairs the pipeline differences between the cohorts.

4.2 Newborns

Across the whole dHCP release the wiring term is $+2.28 \pm 0.46$ against the degree-preserving null and $+4.93 \pm 1.00$ against the annealed one, and gestational age barely moves it. The sample is 524 connectomes built through one pipeline on one atlas [33, 34], spanning 23.0-42.3 weeks of gestational age at birth, with 106 infants born preterm (< 37 weeks) and 50 very preterm (< 32). (The ten neonatal graphs of Table 1 are ten of these 524 at a slightly different threshold, so the two analyses are not independent.) The neonatal results are bounded by the fact that every infant was scanned at or after 37 weeks postmenstrual age (range 37.1-45.1), so the comparison is across brains that completed different amounts of gestation in utero and never follows one brain across gestation. Age at scan is a covariate throughout.

Gestational age explains almost none of it. Against the degree-preserving null the correlation with gestational age at birth (Figure 1, left) is $r = -0.139$ ($p = 0.001$; slope −0.0166 $z$ per week, 95% CI $[-0.0268, -0.0065]$), and partialling out age at scan leaves $r = -0.127$ ($p = 0.004$). Against the annealed null the sign flips: $r = +0.044$ ($p = 0.314$), and by rank correlation $\rho = +0.118$ ($p = 0.007$).

The disagreement is a normaliser artefact, because the denominator of $z$ is set by the graph and the null family, independently of the effect. The annealed null’s ensemble SD is itself correlated with gestational age ($r = -0.135$, $p = 0.002$) where the degree-preserving null’s is not ($r = +0.037$), so that comparison mixes a gradient in the effect with one in the denominator. On the effect scale (the raw NRMSE advantage $\mu - \bar{s}_\omega$, before dividing) the families agree: $r = -0.138$ ($p = 0.002$) and $r = -0.119$ ($p = 0.006$), both surviving age at scan as a covariate ($t = -3.25, -3.10$); partialling the null SD out of $z$ agrees again (Appendix C).

Split at the clinical boundary the difference stays a tenth of a $z$ unit: preterm infants average +2.37 against +2.26 for those born at term ($p = 0.027$, Welch); against the annealed null the split is absent ($p = 0.852$), so it is the weaker of the two readings.

At $n = 524$ this design detects $|r| = 0.12$ at 80% power; the degree-preserving effect-scale estimate exceeds it and the annealed one sits just under it. The wiring effect is therefore present at full size across the entire gestational range and declines slightly with gestational age, consistent in sign across both nulls on the effect scale but worth under 2% of the variance. Its direction is the opposite of a maturational reading: infants who completed less gestation in utero have marginally more of it.

What the wiring term tracks is degree heterogeneity. Across the same 524 graphs it correlates with the small-world index $\sigma = (C/C_{\mathrm{null}})/(L/L_{\mathrm{null}})$ at $r = +0.447$ ($p = 4.4 \times 10^{-27}$), which invites the reading that small-worldness carries it. That reading does not survive decomposing it. The graphs’ own small-worldness, the raw ratio $C/L$, predicts nothing ($r = +0.010$, $p = 0.824$). The zero is a cancellation: clustering and path length each predict it separately and in the same direction ($r = +0.161$; $r = +0.213$), so the ratio carries neither. What does predict it is the coefficient of variation of the degree sequence ($r = -0.402$, $p = 9.3 \times 10^{-22}$); controlling for that roughly halves the apparent $\sigma$ effect ($r = +0.252$); He et al. [30] reach the same variable from the other direction, attributing reservoir memory to hub nodes. The explanation is structural: $\sigma = (C/C_{\mathrm{null}})/(L/L_{\mathrm{null}})$ is itself a real-versus-rewired contrast against the same null family, so at one $N$ and one edge count its variance comes mostly from its normaliser, a function of the degree sequence. The causal claim rests on Section 4.3, where $C$ is manipulated directly.

Gestational age works through the same variable: it predicts $\sigma$ at $r = -0.240$ ($p = 2.8 \times 10^{-8}$; −0.242 partialling out age at scan), in the expected direction, and that explains most of the gestational-age correlation. The structure a fixed reservoir can exploit is already in place across the whole 23.0-42.3 weeks, including in infants born four months early. Gestation does not add to it, and what gestation does change reaches the term mainly through the degree sequence it leaves behind.

4.3 Non-brain graphs

A matched Watts-Strogatz graph reaches the newborn connectome’s wiring term, so what a fixed reservoir gains from wiring is not particular to brains. Since generic topology already shapes reservoir performance (Section 2), the control a connectome claim needs is a matched non-brain graph, and it has not been run.

Figure 2 stops the developmental result being read as a claim about brains specifically, though not in the way we expected: the two nulls disagree, and the disagreement is informative. Matching on $N$, edge count, weight multiset and strength sequence, and pairing at the level of the 5 templates: against the degree-preserving null no family reproduces the real neonatal value, because a Watts-Strogatz graph exceeds it by +0.89 (95% CI [+0.50, +1.27]) while a random geometric graph falls short by −1.08 and a non-spatial block model by −1.51. Against the annealed null the same two families are both statistically indistinguishable from the connectome (−0.16, CI [−0.57, +0.25]; +0.01, CI [−1.04, +1.07]), and only the block model is excluded (−3.36, CI [−4.10, −2.62]). “Indistinguishable” is the acceptance of a null: at 5 templates the equivalence margin is 0.47 $z$ for Watts-Strogatz and 0.82 for random geometric, so the acceptance measures resolution at this sample size and is no evidence of equality.

Two things survive that disagreement. The non-spatial block model is excluded under both nulls; and under neither does the connectome beat a matched small-world graph, the family on which the mechanism rests. Which families count as matches depends on the null, so no single-null comparison settles whether the connectome is special. One caveat bounds the size of the Watts-Strogatz margin: the families are not matched on degree heterogeneity, a strong correlate of the wiring term, and the mismatch runs the convenient way (Appendix D). We therefore rest on the weaker claim the question actually asks, that non-brain graphs reach the connectome’s value, and leave the size of the excess uninterpreted.

Manipulating small-worldness over near-uniform degrees does carry the effect. Sweeping the Watts-Strogatz rewiring probability with size, edge count, weight multiset and strength sequence held fixed moves a graph from lattice through small-world to random, and the effect follows: over 5 templates × 9 probabilities × 3 draws, $z_{\mathrm{wiring}} = +3.18 \pm 0.38$ where $\sigma > 1.9$ ($n = 90$) against $+0.08 \pm 0.22$ where $\sigma < 1.3$ ($n = 30$; the 15 cells between are unbinned; Figure 2, bottom). Destroying small-worldness abolishes the effect. The continuous version of the binned contrast is not available, and the cross-graph correlation over the real graphs looks stronger but is confounded with cohort (Appendix D).

5 Limitations

Only NARMA-10 ran at 200 graphs; $\mathrm{MC}_{\mathrm{lin}}$ remains at five. Every infant was scanned at or after 37 weeks, the preterm ones after postnatal experience, so none of this measures structure before experience, and conclusions concern undirected, unsigned connectomes only. Fixed $N$, fixed edges and $\lambda_{\max}$ rescaling put density and strength growth beyond the wiring term’s reach (failed routes: Appendix E).

Two operating points qualify every result, both found in Appendix B. Over 6 values of $\rho_W$ the shares move but the sign does not: the wiring term is positive in 231 of 240 cells, and at $\rho_W = 0.5$ the naive statistic finds nothing (+0.02) where the wiring term is +0.27, so weight placement was masking an effect there. The ridge matters more: it is an absolute constant on a Gram matrix whose scale (2) leaves free, so this readout is effectively unregularised, identically for every substrate, and regularising it collapses the degree-preserving wiring term (it falls below $z = 1.96$ at a ridge of 0.0001, itself still a negligible relative regularisation on this Gram matrix) where the annealed one holds up much better, a qualifier any reading of the neonatal result should carry.

6 Discussion

Published effects measured against degree-preserving or rank-matched nulls need re-reading through (1), and (2) says why what it removes is large: rescaling pins $\lambda_{\max}$ and leaves $\lVert W \rVert_F$ free, so redealing the weight multiset moves the reservoir’s effective gain and leaves its topology alone. The term is therefore a perturbation of the operating point and has no fixed sign: it inflates the naive effect at $\rho_W = 0.95$ and masks one at 0.5, so it must be measured where the reservoir is run, averaged over the weight rule.

For comparisons between empirical networks and rewired null models, we recommend a simple reporting procedure. The empirical wiring should be evaluated under the null model’s own weight rule and averaged over at least 25 draws, with the resulting wiring term reported together with its Monte Carlo error. The contribution of weight placement should be reported separately, rather than combining the two effects into a single $z$. Claims of network-specific structure should be supported by applying the same analysis to a non-brain graph matched in size, edge count, weight multiset and strength sequence, using the same null models throughout.

Degree heterogeneity predicts the surviving term across graphs (Section 4.2), but it cannot be what that term measures within one: the null fixes every node’s degree, so hubs stand in both arms. What the Watts-Strogatz sweep manipulates, clustering at short path length over near-uniform degrees, does carry it.

The newborn connectome has what a correct null detects at every age, and a matched small-world graph reaches that value, so the effect is no evidence that evolution specifies a particular wiring diagram. For the genomic bottleneck [2] the useful part is then specifiable by a few statistics; for a learner, a connectome buys nothing over such a graph [3].

This post carries the paper’s main body. Appendices A to G — battery and inference details, operating-point sweeps, null-model anatomy, synthetic-family details, mediation and results that do not reproduce, ethics and data, and reproducibility — are in the attached PDF, together with Figures 3 to 5 and Table 2.