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Under review as a conference paper at ICLR 2027

Preprocessing Sensitivity as a Signal in Brain Representations

Abstract

We treat a brain representation's response to preprocessing as an observable feature in its own right. For fMRI, we measure how a joint time-delay spectral score changes when five selected aCompCor nuisance regressors are added to the same recording. The score measures excess concentration in two leading modes relative to channelwise phase-randomized references. In a post hoc analysis of 201 Alzheimer's Disease Neuroimaging Initiative participants, this paired response has an estimated adjusted slope of +0.472 percentage points per point of clinical severity (CDR-SB; HC3 standard error 0.247), while the original baseline score has no established association. The response coefficient remains similar when common temporal regressors change both pipelines' absolute scores, in a sensitivity analysis on the same cohort. We then characterize what this response can identify. A Gaussian construction shows that a related population statistic detects collective changes while every channel's complete univariate law remains fixed. Yet observation changes alone can produce a nonmonotone response at fixed latent dynamics. Observationally identical models further show that no decoder of the same inputs can resolve the latent source without additional assumptions. Five controlled simulation families connect these mechanisms to the finite-sample spectral measurement. Together, the findings make preprocessing response a concrete target for representation analysis, linking an estimated clinical association to explicit limits on latent interpretation.

Primary area:
applications to neuroscience & cognitive science
Keywords:
preprocessing, Alzheimer's disease, neuroimaging

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_QMpYOpenReview ↗
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Paper summary

This paper treats the response to a specified preprocessing operation as a measurable property of a brain representation. Its main statistic contrasts a delay-embedding spectral score before and after adding five aCompCor regressors, with scores referenced to channelwise phase-randomized signals. A post hoc ADNI analysis relates this paired response to clinical status, with a common-DCT sensitivity analysis on the same participants. Analytical constructions and simulations characterize sensitivity to joint organization and observation changes. A complementary analysis studies windowed functional-connectivity dispersion in future CDR-SB prediction, including an exploratory preprocessing-response comparison.

Critical strengths
  1. The paper defines a testable measurement rather than treating preprocessing sensitivity only as an informal robustness concern. Specifying the operator, representation statistic, and paired contrast makes the question concrete. The paired analysis retains the relationship between the two preprocessing branches, and the common-DCT control helps distinguish the added regressors from differences in temporal nuisance modeling. This is a useful methodological framing.

  2. The controlled analysis gives the measurement an appropriately limited interpretation. The constructions show sensitivity to joint structure with fixed channelwise laws, while observation changes can also affect the statistic. The paper therefore avoids equating sensitivity to collective organization with identification of a neural source. These limits are consequential because they prevent a clinical association from being overinterpreted as a biological mechanism.

Critical weaknesses
  1. The response-specific empirical advance is limited in scope. The paired analysis reports an estimated positive association between clinical severity and the response of one spectral score to one specified preprocessing change. However, the main finding was developed post hoc in a single ADNI cohort. The common-DCT analysis strengthens that finding under an additional shared nuisance control, while retaining the same participants and the other measurement choices. The prognostic results in Section 6.4 primarily support window-FC dispersion, and Appendix M.4 provides an additional exploratory response comparison; neither independently validates the main spectral response. Together, these analyses support an interesting measurement case study, but the additional scientific understanding established by treating preprocessing response as a feature remains modest. This limited scope weakens the significance of the empirical contribution.

  2. The formal analysis provides useful interpretive safeguards, but its methodological contribution remains modest. Proposition 1 establishes collective sensitivity by changing zero-lag spatial correlation while preserving the individual channel laws. This demonstrates the value of a joint observable over univariate summaries, but does not distinguish the delayed construction from sensitivity already available in joint covariance. The turnover and alias constructions explain why a score increase need not indicate better signal preservation and why identical observations cannot identify the latent source. These are valid and consequential limits. However, with the delay embedding and spectral score themselves acknowledged as established constructions, the formal contribution is principally a characterization of the selected measurement and its interpretive boundaries. I am not persuaded that linking these results provides a sufficiently substantial methodological advance to support acceptance.

Questions for authors
  1. How should the stability under common DCT be interpreted alongside the individual branch associations? Table 1 reports similar paired clinical coefficients under the original and common-DCT designs, while Section 6.2 reports changes in absolute score levels. Please provide the BASE and A5 clinical coefficients under both designs, with their joint uncertainty, alongside the paired coefficients. Does the contrast preserve a clinical relationship that changes substantially at the branch level, or are the branch associations also stable while their score levels shift? Either pattern is compatible with a valid paired finding, but the distinction would clarify what the DCT control adds to the argument for treating preprocessing response as a separate feature.

  2. Which measurement insight from the theoretical analysis extends beyond this particular score? Proposition 1 varies zero-lag spatial correlation while preserving the marginal laws, and Proposition 2 explains observation-only turnover through normalized spectral concentration. Which conclusions depend specifically on the delayed, phase-referenced construction, and which also apply to simpler normalized joint-covariance responses? Please state the transferable measurement principle, its assumptions, and the proposition or controlled result that supports it. If the intended contribution is instead the characterization of this particular observable, please explain what that characterization adds to interpreting the clinical response. This would help assess the scope and significance of the contribution without making a new experiment a prerequisite.

  3. Which appendices do the two unresolved “Appendix ??” references point to? On p. 6, line 320, the reference is meant to identify the checked inputs and numerical discrepancies for the independent numerical reconstruction. On p. 10, line 492, it is meant to distinguish public execution from the restricted clinical pipeline and document independent numerical checks. Please provide the exact appendix or subsection number and page range for each reference, and clarify which reported checks each location supports. These references are needed to locate the evidence for the numerical verification and understand the scope of reproducibility from the public materials.

1 comment

Thank you for the precise questions. Common DCT shifts the absolute score levels, while the BASE, A5 and paired slope estimates remain similar.

The submitted aggregate_results.json gives these slopes (HC3 SE), in percentage points of JJ per CDR-SB point:

DesignBASEA5A5−BASE\mathrm{A5}-\mathrm{BASE}
Original-0.0443 (0.2493)0.4279 (0.2876)0.4722 (0.2470)
Common DCT-0.0315 (0.2189)0.4326 (0.1910)0.4641 (0.2210)

The joint HC3 covariance matrices for [BASE,A5][\mathrm{BASE},\mathrm{A5}], in squared slope units, are:

\begin{bmatrix} 0.062155 & 0.041933 \\ 0.041933 & 0.082716 \end{bmatrix}, \qquad \text{Common DCT:}\quad \begin{bmatrix} 0.047915 & 0.017783 \\ 0.017783 & 0.036476 \end{bmatrix}.$$ The paired SE retains the positive branch covariance. For this response, we additionally reconstructed cross-design uncertainty from the unchanged archived 201-person cohort. DCT-minus-original slope changes (HC3 SE) are $+0.0128$ (0.1551) for BASE, $+0.0046$ (0.1793) for A5, and $-0.0081$ (0.0904) for the response. These are descriptive checks, not equivalence tests or independent validation. Mean $J$ changes from 16.415 to 15.286 for BASE and 13.794 to 12.229 for A5. DCT addresses a shared temporal-nuisance concern; it does not show unique stability of the contrast. Proposition 1 characterizes collective sensitivity by varying zero-lag correlation while preserving each channel's entire Gaussian marginal law. Static covariance also detects this change. The contribution is the exact response of the chosen population observable, its connection to finite-sample measurements, and the resulting interpretation of the clinical association. A transferable principle follows from Proposition 2. Take mutually independent, unit-variance processes $Z_i$, $U$ and $V$ with the same autocovariance. The channels are $X_i=Z_i+\sqrt{s}\,U$ and the proxy is $W=U+\tau V$, with $s>0$ and $\tau>0$. Writing $t=\tau^2/(1+\tau^2)$, normalized correlations before and after regression are $$r_0= \frac{s}{1+s},\qquad r_A=\frac{ts}{1+ts}.$$ For any continuous strictly increasing $g:[0,1]\to\mathbb{R}$, the response $g(r_A)-g(r_0)$ is negative for finite $s>0$ and approaches zero both as $s$ approaches zero and as $s$ grows without bound. It is therefore nonmonotone in shared observation noise despite fixed latent dynamics. This also applies to suitable normalized static-covariance scores. The particular rational formulas require the stated spectral eigenvalue branch; the turnover principle does not require delays or phase references. The alias result applies to every decoder of identical observed fields and proxies within the stated model class: different designated latent targets remain indistinguishable. Source attribution therefore needs additional identifying assumptions or measurements. This explains why a severity association or larger score cannot alone identify preserved neural signal. The clinical finding remains post hoc; the separate FC-dispersion prediction addresses a complementary endpoint. This person-level response and its identification boundary complement [pipeline multiverse sensitivity analysis](https://doi.org/10.1162/imag_a_00523) and [pipeline-invariant representations](https://arxiv.org/abs/2208.12909). Both broken references point to an omitted reproducibility section; we apologize. There is no corresponding appendix page in the submitted PDF. For p.6, line 320: original-score reconstruction agrees within $8.89\times10^{-16}$; 47 synthetic checks qualified the DCT adapter; separate OLS/HC3 reconstruction of all 20k bootstrap draws agrees within $6.23\times10^{-14}$. Direct Hankel/SVD checks cover four prespecified records (DCT counts 3,5,8,9; lengths 97,139,197,214), all 199 references in both branches, within $1.27\times10^{-13}$. Controlled-world checks cover 800 summaries and 160 complete scores. These verify implementation, not clinical replication. For p.10, line 492: public verify.py checks synthetic inputs, reconstruct.py reconstructs aggregate displays, and synthetic/reproduce.py with compare_synthetic.py reproduces controlled worlds. Human replication requires authorized ADNI inputs and Appendices B–E, pp.17–21. The restricted clinical pipeline and participant ledgers are not distributed.
Reviewer_1p2uOpenReview ↗
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Paper summary

This paper discusses the use of fMRI preprocessing sensitivity as a feature on its own and explores its relations with clinical measures in ANDI dataset. The authors report an association with disease severity and use theoretical analysis and simulations to examine what preprocessing sensitivity reveal about underlying brain dynamics.

Critical strengths

The paper approaches preprocessing from an interesting perspective in treating its sensitivity as a measure/feature and examining its association with clinical severity. The authors are transparent about the explorative nature of the findings and its limitations.

Critical weaknesses
  1. Regarding clinical association, the paper progresses from a non significant association in the original analysis to a significant paired preprocessing response, then a DCT sensitivity analysis, all under the same 201 participants. It is, as the authors acknowledged, a post hoc finding with the original branch results known (Appendix H). Although the DCT analysis shows a similar association, it does not serve as independent validation. The paper suggests that preprocessing sensitivity contains clinically relevant information, but it is unclear whether this finding is data dependent and generalises beyond the tested cohort.

  2. The spectral response depends on a few parameters that are fixed but not sufficiently justified or evaluated for sensitivity. 1) Hankel embedding length L = 10, it is unclear whether the autocorrelation structure of the BOLD signals was considered in this choice; 2) the two leading singular modes for computing spectral concentration; 3) five aCompCor components (Sections 3 & 5). Could the authors clarify the rationale for these choices and evaluate or discuss the sensitivity of empirical clinical association to these parameters?

  3. Paper’s analysis (Fig 3) shows preprocessing response can change with the observation model with fixed latent dynamics. This potentially poses a concern for clinical association, given atrophy and tissue composition may affect the signals captured by aCompCor components. The clinical adjustment does not account for these although motion and quality covariates are in place.

  4. The paper is quite difficult to read; it would benefit from enhanced clarity and a clearer highlighting of the main contributions, the connection between the different analyses. There are also several unresolved appendix references in the text (‘Appendix ??’).

Questions for authors

Is there any independent cohort available for the authors to test the fixed contrast? Could the authors evaluate or discuss the fixed parameter choices?

2 comments

Thank you for the careful review. The study makes preprocessing response a participant-level feature and connects its clinical association to an explicit measurement model. The paired slope is 0.472 percentage points per CDR-SB point (HC3 SE 0.247), and remains 0.464 (SE 0.221) when a common temporal basis changes both pipelines' absolute score levels. This supports stability under that nuisance specification within this cohort.

Access to suitable imaging and clinical records constrains the available sample. We used the eligible 201-person ADNI cohort for paired inference with shared clinical adjustment, a common temporal-nuisance control, and the complete sensitivity grid below. The initial BASE association was not statistically established, and the paired response was developed after the branch results were known. These same-cohort checks provide exploratory evidence about specification dependence, with the documented bootstrap calibration limits. The fixed contrast is a concrete target for independent validation. The separate future-CDR analysis evaluates window-FC dispersion in a complementary predictive task; it does not validate the spectral response.

The parameters define a reproducible observable. L=10L=10 at TR=3\mathrm{TR}=3 seconds spans delays from 0 through 27 seconds; it specifies a measurement scale rather than an established optimal BOLD autocorrelation timescale. The two-mode fraction is a fixed low-rank concentration summary. Five aCompCor components define the added nuisance subspace, selected from the combined mask by the documented singular-value ordering.

For this response, we recomputed a descriptive sensitivity grid on the unchanged 201 common-DCT participants, retaining the clinical model and all 199 phase-reference draws. Before examining outcomes we fixed L∈{1,5,10,20}L\in\{1,5,10,20\} and leading-mode counts k∈{1,2,3}k\in\{1,2,3\}. All paired slopes (HC3 SE), in percentage points per CDR-SB point, are:

Delay lengthk=1k=1k=2k=2k=3k=3
L=10.315 (0.244)0.028 (0.164)-0.043 (0.118)
L=50.481 (0.196)0.586 (0.257)0.335 (0.202)
L=100.297 (0.123)0.464 (0.221)0.425 (0.213)
L=200.188 (0.082)0.300 (0.155)0.290 (0.162)

All nine delayed settings have positive point estimates. L=1L=1 is the exact phase-referenced static-covariance counterpart, with its k=2k=2 estimate close to zero here. The other static mode counts show why this cannot be generalized to every static statistic. We report every setting without selecting a preferred one. The delayed estimates support a response extending beyond exactly L=10L=10 and k=2k=2. The sweep holds the aCompCor rank at five.

Atrophy and tissue composition may change the proxy signals and the effective subspace removed by aCompCor. Motion and quality adjustment does not isolate these effects. Figure 3 makes the concern explicit: observation changes can alter the response at fixed latent dynamics. It does not establish that this mechanism explains the ADNI association. We interpret ΔJ\Delta J as the response to a specified nuisance operation; biological attribution additionally requires evidence about the proxy–source relation, such as external physiology or a justified exclusion assumption.

The theoretical and empirical parts therefore work together. Joint organization can change while complete univariate laws stay fixed, yet the response cannot itself quantify neural preservation. The exact alias example explains why a more powerful decoder of the same inputs cannot resolve the source ambiguity. This supplies both a measurement interpretation of the association and the conditions needed to take its biological interpretation further.

Both unresolved references point to the intended “Reproducibility artifacts and verification scope” section, omitted from the compiled submission. We apologize and supply the relevant scope here: the public repository provides portable measurements, aggregate reconstruction and controlled-world checks; human fits require authorized ADNI inputs and the declared cohort and inference contracts. Numerical agreement is implementation verification, not clinical replication. We will restore the section and clarify the roles of the clinical association, controlled interpretation and complementary prognostic task in the main text.

Thank you so much for the authors' response. My main concerns around independent clinical validation and the potential influence of atrophy and tissue composition remain, and with careful consideration, I would like to maintain my original ratings. Many thanks for the authors' time and efforts.

Reviewer_277DOpenReview ↗
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Paper summary

This article tackles an important issue, the sensitivity to preprocessing pipelines in neuroimaging. Despite being neuroimaging-centered the ideas might span across other fields where data pre-processing is critical and not yet established.

To tackle this problem the authors focus on one signal type the fMRI signal, specifically per functional network and an operator response formalism to evaluate preprocessing pipelines. Furthermore this work also relates to long-standing questions in the ICLR community (and related communities) such as causal learning, as the preprocessing pipelines have a causal influence on the resulting signals. Furhtermore, they argue that in this case pipeline identifyability is not prioritary.

The authors do not rank pipelines. Their work is on a formalism that's able to evaluate changes in the preprocessing pipeline as an operator response. Specifically, the change in the score of a representation when a nuisance-regression operator replaces another in the same data or recording. The operator response is then related to alzheimer's diagnosis via a regression on the CDR-SB marker.

As a full disclaimer I think that the paper should stand on it's own without the supplementary materials and that these are to clarify. So I'm evaluating the article paying attention almost exclusively to the 8 main pages.

Critical strengths
  • The whole measurement system through the Hankel matrices is sound and well-posed. Making a pipeline change into a measurable object is useful and could turn the issue into a differentiable selection process as a consequence if the field takes note of the work and it generalises well.
  • Section 3 is well worked and clearly described as the experimental baselines are.
  • The inference pipeline is well described.
  • The evaluation on specific problems in neuroimaging is well carried out, albeit a bit difficult to understand for a non-versed audience.
Critical weaknesses
  • the way that results are written is generally very hard to follow.
  • the interpretability of the ΔJ\Delta J , the present framework does not allow to check if the changes track atrophy, or CSF volume fraction during motion, this should be stated clearly.
  • There is no baseline for ΔFC\Delta FC and no weep over the parameter L. If J detects linear cross-channel organization, this should be tested against a static counterpart
  • The main result or empirical claim is not shown at conventional significance. Table 1 reports a paired slope of .472 with an HC3 std error (SE) of 0.247. This slope is at least 2 standard errors from 0, which includes the 0 slope in that interval. The common-DCT with .464 (SE .221) is very close to this condition too. Furthermore, the wild-bootstrap seems to over-reject in the small tail. Authors might need to re-adjust their significance procedure, as if not, most results become suggestions.
Questions for authors
  • Can you provide more insights on the interpretability of ΔJ\Delta J or it's lack of identifyiability ? I think that it would be a good contribution to the field
  • Can you make a comments towards the generalization of the operator-response approach beyond the aCompCor nuisance incorporation to the pipeline?
  • Can the S.E. bars be made smaller such that the main results hold better?
1 comment

Thank you for recognizing the value of making preprocessing responses measurable. The paper connects a clinical observation to a practical question: what information does a representation's response to preprocessing carry, and what can that tell us about the underlying signal?

ΔJ\Delta J measures how adding the specified aCompCor subspace changes excess joint spectral concentration in the same recording. A positive severity coefficient means that this change becomes more positive with CDR-SB after adjustment. The mean response is negative, while its severity slope is positive. This does not quantify removed neural signal or rank biological quality. Atrophy, CSF fraction and tissue composition could influence both the nuisance components and the response; motion and quality adjustment does not exclude these explanations. We agree that this belongs in the main text.

The theory explains why this distinction matters. Proposition 1 establishes sensitivity to joint organization while every channel's complete marginal law remains fixed. Proposition 2 shows observation-only turnover at fixed latent dynamics. The alias construction then gives identical observed fields and proxies with different designated latent sources: a decoder of those inputs cannot resolve the ambiguity without additional assumptions or measurements. These results give the clinical response a precise measurement interpretation and explain why increasing JJ cannot itself establish better neural preservation.

The uncertainty deserves a direct answer. The original estimate 0.472 with HC3 SE 0.247 has an approximate normal-reference 95% interval of [−0.012,0.956][-0.012,0.956] percentage points per CDR-SB point; common DCT gives [0.031,0.897][0.031,0.897]. The reported bootstrap pp-values use a different, approximate reference distribution. Its documented small-tail over-rejection prevents treating p=0.0076p=0.0076 as calibrated 1% confirmation. The analysis is post hoc, and DCT reuses the same 201 participants. Within this eligible cohort, the positive response estimate remains similar under a motivated temporal control, with uncertainty quantified by these intervals.

The precision checks also clarify the error bars: common-DCT phase Monte Carlo SE is 0.0038, versus participant-sampling SE 0.221. More phase references would therefore make little difference to clinical uncertainty. The remaining uncertainty is mainly participant sampling, which additional independent participants would help reduce. The estimate remains near 0.46 when the common temporal basis changes both pipelines' scores. Joint fitting addresses the known possibility that sequential filtering and regression reintroduce removed components (Lindquist et al., 2019).

For your static and LL comparisons, we recomputed a sensitivity grid for this response on the unchanged 201 common-DCT participants, retaining the clinical model and all 199 phase-reference draws. Before examining outcomes we fixed L∈{1,5,10,20}L\in\{1,5,10,20\} and k∈{1,2,3}k\in\{1,2,3\} leading modes. For the submitted k=2k=2 score, paired slopes (HC3 SE) are respectively 0.028 (0.164)0.028\,(0.164), 0.586 (0.257)0.586\,(0.257), 0.464 (0.221)0.464\,(0.221), 0.300 (0.155)0.300\,(0.155). All nine delayed settings have positive point estimates; the three static estimates are 0.315 (0.244)0.315\,(0.244), 0.028 (0.164)0.028\,(0.164), −0.043 (0.118)-0.043\,(0.118). We retain every setting without selecting a new preferred specification.

L=1L=1 is the exact phase-referenced static-covariance counterpart of this concentration score. These exploratory results support examining delay structure here, without establishing superiority over arbitrary static ΔFC\Delta\mathrm{FC} features or independent clinical validation. Proposition 1 likewise changes zero-lag correlation and does not establish information beyond static covariance. At TR=3\mathrm{TR}=3 seconds, L=10L=10 spans 0–27 seconds, defining a measurement scale rather than an optimal BOLD timescale.

The operator-response principle extends to another specified operator pair: hold the recording, temporal support, representation and reference rule fixed, compute the paired change, and evaluate it against the relevant endpoint. The nested-projection energy identity specifically requires the regression structure used here and does not automatically extend to censoring or non-nested operations. This gives a concrete way to study preprocessing sensitivity while keeping clinical information and biological interpretation distinct.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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