u/ITheClixs

I’ve been working on an identification problem in cross-asset market impact, and I’d be interested in having people here try to break the argument.
The motivating observation is pretty uncomfortable.
In one published one-minute cross-asset return-on-flow specification that motivated this project, the mean estimated cross-asset coefficient is positive. After adding a single cross-sectional principal-component control, the mean changes sign and the fraction of negative coefficients changes dramatically.
That raises a basic question:
When we regress asset returns on contemporaneous order flow across many assets, under what assumptions can the off-diagonal coefficients actually be interpreted as structural cross-impact?
I considered the simultaneous system
r_t = Lambda q_t + Gamma f_t + u_t
q_t = B r_t + Delta_f f_t + v_t
where:
Lambda = structural price-impact matrix
f_t = K latent common factors
B = same-bin return/flow feedback
Gamma and Delta_f = factor loadings
If A denotes the population coefficient matrix obtained by regressing returns on flows, then
A = Lambda + G
where G is the confounding gap.
The first result is that
rank(G) <= K + rank(B).
So latent commonality does not produce arbitrary estimation error. It produces a structured, low-rank distortion.
But low rank does not mean small.
If feedback is absent and the true structural impact matrix Lambda is diagonal, then the entire estimated matrix must lie in
D_K = { D + R : D diagonal, rank(R) <= K }.
In other words, a purely diagonal structural model can generate a dense-looking cross-impact matrix whose off-diagonal entries are comparable in magnitude to genuine own-impact.
That led me to what I think is the more important result:
Lambda is generally set-identified rather than point-identified from the relevant second moments.
There is a family of different structural impact matrices that reproduce exactly the same observable second moments after changing the latent-factor channel appropriately.
So controlling for a factor does not necessarily “remove the confounding and reveal the structural matrix.” It can move the estimate along the confounding directions without selecting the true structural matrix.
In a permutation-invariant one-factor geometry, I can solve the identified set analytically. At the calibration I’m using, the sharp interval for the structural off-diagonal coefficient contains zero, and its half-width is roughly 7.4 to 8.9 times the observed cross-impact coefficient.
So in that case the data do not identify even the sign of structural cross-impact.
What surprised me more is what happens to execution costs.
Suppose a desk evaluates a trade x using quadratic execution cost
C(x, M) = x' M x.
Then using the regression matrix instead of the structural matrix produces error
x' G x.
Since G is low rank, the error itself has low-dimensional structure.
There is therefore a large set of directions that are immune to the confounding. But this does not mean a randomly chosen trade is approximately safe.
In the registered N=30, K=3 known-truth experiment, an equal-weight index basket is mispriced by about 54% while a particular dollar-neutral basket has exactly zero error.
The dollar-neutral result is geometry-specific, though. In the general model, dollar neutrality by itself does not imply immunity. The relevant object is the null structure of the confounding gap.
This suggests an odd distinction:
The impact matrix can be unidentified while the execution cost of a particular trade is point-identified.
I also wanted the theory to be falsifiable rather than just saying “maybe factors explain everything.”
So I defined a normalized distance from an estimated impact matrix to the diagonal-plus-rank-K variety:
psi_K(A) = distance(A, D + rank-K matrices) / norm(offdiag(A)).
Under the pure-confounding null, the population value is zero.
A materially nonzero value therefore rejects the maintained model consisting of diagonal structural impact, no feedback, K factors, and the accompanying covariance assumptions.
Importantly, psi_K = 0 does not prove that structural cross-impact is absent. The test is one-sided in interpretation: it can falsify the pure-confounding model but cannot confirm it.
The finite-sample behavior is also not magically nice. In simulations the plug-in bootstrap over-rejects badly at small T and only starts controlling a nominal 5% size around roughly
T >= 5 N^2.
I tried a simple degrees-of-freedom variance correction and it completely failed because the bootstrap problem is primarily mis-centering rather than insufficient dispersion.
The theoretical/known-truth stage is preregistered. For the main verification I used
N = 30
K = 3
T = 10,000,000
and checked 1,800 coefficient targets. The maximum relative discrepancies against the population formulas were below the preregistered 0.001 gate.
One important caveat: I have not yet used the external market dataset for the registered empirical test. The current version is deliberately a pre-results manuscript for that stage. So I’m not claiming that real cross-impact is spurious. The claim at this point is an identification result plus a falsifiable empirical design.
Repo / preprint / derivations / preregistration / code:
https://github.com/ITheClixs/spurious-or-structural
The questions I’d particularly like criticism on are:
Is there a structural restriction used in actual market-impact work that defeats the set-identification argument without simply assuming the answer?
Does the low-rank characterization miss an economically important confounding channel that would change the rank bound?
Is distance to the diagonal-plus-low-rank set the right object to test, or is there a better way to formulate the falsification problem?
For people who work with institutional flow or market-impact estimation: what empirical result would actually convince you that an observed off-diagonal coefficient is structural rather than common-flow contamination?
I’m especially interested in counterexamples. If the identification argument breaks under a realistic microstructure assumption, that’s more useful to me than agreement.

I’ve been looking at a fairly basic question in weight-space learning that I don’t think gets separated cleanly enough:
Why does reading semantics directly from neural network weights work pretty well when the networks share an initialization, but collapse when the networks are fitted independently?
The usual explanation is parameter symmetry. Permute hidden units, flip equivalent signs, etc., and two parameter vectors can represent the same function while looking completely different to a downstream model.
But there are actually several different claims hiding in that explanation:
the parameterization has a symmetry group,
accounting for that symmetry improves weight-space prediction,
the symmetry is actually sufficient to explain the observed degradation between shared-init and independently fitted networks.
Those aren’t equivalent, so I tried to measure them separately.
The setting is SIREN-style implicit neural representations.
For a hidden sine neuron, the relevant function-preserving transformations generate the infinite dihedral group
D_inf = Z semidirect_product Z_2
and including neuron permutations gives the layer action
D_inf wr S_n.
For one hidden layer, I prove generic identifiability modulo this group using the distributional Fourier transform of the realized function.
Roughly, the Fourier transform becomes an atomic measure supported at the incoming frequencies +/- w_i, which lets you recover the parameters up to exactly the D_inf wr S_n action under explicit genericity conditions.
One consequence is that this isn’t just the usual permutation/sign story. Integer-pi phase transformations are affine rather than linear, so they aren’t captured by symmetry descriptions restricted to monomial matrix actions.
At depth two things get more annoying because a neuron’s outgoing weights are simultaneously acted on by the next layer. I ended up constructing exact cross-layer invariants by coupling the layers through the second-layer Gram matrix instead of treating neurons independently.
The empirical part then uses roughly 1.8 million fitted INRs across MNIST, FashionMNIST, and CIFAR-10, with controlled protocols separating shared initialization, optimization stochasticity, and independent initialization.
The result I found most interesting:
Randomizing only the exact symmetry group, while keeping each network’s represented function fixed, destroys 79.1 of the 80.4 accuracy points in the MNIST shared-init vs. random-init gap.
I want to be careful about the interpretation here.
This establishes sufficiency: symmetry scatter alone can reproduce almost the entire degradation.
It does not establish that 79.1 / 80.4 of the naturally occurring gap is causally mediated by symmetry. Those are different estimands.
Breaking the group apart, sign flips account for roughly 63 points of that induced loss, neuron relabeling about 15, and integer phase shifts about 1.
There was another result that changed my interpretation of the problem quite a bit.
A reader that directly quotients the D_inf wr S_n structure on the raw parameters reaches 0.917, compared with:
0.628 for the best orbit-valued reframing,
0.526 for the same reader family over a fixed invariant encoding,
0.265 for a permutation-equivariant baseline.
But when I FLOPs-match weight-space inference against simply querying the INR as a function, the function-space route is still much better:
95.3% at 1.6 MFLOP using 64 learned query coordinates
versus
64.4% at 5.5 MFLOP for the best weight-space rung on that frontier.
That leads to what I think is the more interesting conceptual question:
If a complete invariant is informationally equivalent to access to the realized function, then the strongest justification for operating directly in weight space may ultimately have to be computational rather than informational.
Everything is public here:
https://github.com/ITheClixs/project-siren-gap
The repo includes the paper, implementation, tests, pre-registrations, lab notebook, prediction ledger, claims ledger, and experimental results.
I’d particularly appreciate criticism on three things:
whether the sufficiency/mediation distinction is being drawn correctly,
whether anyone sees a counterexample or missing assumption in the one-hidden-layer maximality argument,
whether there is related work on affine symmetry groups of periodic-activation networks that I’m missing.
Also very interested in attempts to break the invariants or reproduce the group-randomization result.
If something here is wrong, I’d rather find out from someone trying to kill it.