acceptodds
Under review as a conference paper at ICLR 2027

CertifyPAR: Adequacy Certification and Coefficient Inference for Piecewise Affine Regression

Abstract

Precise coefficient estimates in piecewise affine regression do not establish that a common affine description is adequate within each region. We introduce Certify-PAR, a reporting contract that certifies regional affine adequacy before releasing coefficients with valid confidence intervals. Existing learners supply regions fixed independently of the audit responses; coefficients are estimated anew from the au- dit data. The targets are least-squares projection coefficients on the observed audit inputs, defined without assuming an affine mean. In the two-axis construction, two equivalence tests assess non-affinity within prespecified sub-regions (audit cells) and disagreement among their affine projections. Both noise-normalized root-mean-square departures must be certified below their respective prespecified margins. A pooled alternative certifies total departure from a common affine fit. In either construction, a region’s requested coefficients are released together only after certification. Under independent homoskedastic Gaussian errors, certification based on audit residual projections preserves the coefficient-error distribution while reusing audit observations for estimation. For unknown error variance, two pure-error samples, independent of each other and the audit data, provide separate certification and inference scales. Under these assumptions, we establish finite-sample control of the familywise false-certification probability and, separately, simultaneous confidence-interval coverage conditional on every complete report- ing pattern of positive probability. Simulations using synthetic data and real-data covariates assess error control under the assumed noise model and quantify trade- offs among reporting availability, coefficient precision, and measurement cost. GPU-runtime and fluorescence-calibration examples illustrate reporting decisions under benchmark adequacy margins and highlight obstacles to satisfying the noise assumptions required for exact guarantees.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
uncertainty quantification, piecewise affine regression, equivalence testing, post-selection inference, model auditing

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_5oDJOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes CertifyPAR, a method for deciding when the coefficients of a piecewise affine regression model are reliable enough to report. It first checks whether one affine model is a good enough description of each region, because a coefficient can be estimated very precisely even when the regional model itself is misleading. Under its Gaussian noise assumptions, the author proves that this checking step can be combined with coefficient estimation, while still keeping valid confidence intervals and controlling false certification. Extensive experiments show that the method keeps error rates near their targets and is able to avoid reporting misleading coefficient. It also give narrower intervals than splitting the data.

Critical strengths

The strengths of this paper, according to me, are as follows:

  • The paper solves a real gap between "precise" and "trustworthy" coefficients. As a narrow confidence interval cannot tell us whether one affine model is actually a good representation of the whole region, CertifyPAR straight up addresses this question before reporting the coefficient. I think this is a strong and valid point, as it addresses the failure mode that ordinary regional regression can miss: the model can have excellent predictive fit, or a very precise slope, while still averaging over different local behaviors.
  • The two main guarantees are, as far as I understand, correct and strong. The authors are able to provide control over the probability of falsely verifying an inadequate region and the confidence interval error after the reporting decision. This separation is important because the reporting decision can distort inference. As the authors show, the adequacy decision uses residual information while the coefficient estimate depends on an orthogonal part of the data. Thus, an exact finite-sample argument under the stated model is derived. I consider this a strong contribution, because post-selection/post-screening inference is where otherwise good procedures become invalid.
  • A simple way to avoid selection bias is to split the data, one part to decide whether to report and another part to estimate the coefficient. CertifyPAR shows that this split is not needed. Indeed, the experiments show that this mechanism of reusing the same data improves efficiency. I would say it is a very elegant result.
  • The experiments are broad and transparent, and matches the claims that the authors made well enough. I recognize and appreciate the authors' effort put into all these validations.
Critical weaknesses
  • My main concern with the paper is rather obvious: is the assumption of independent and homoskedastic Gaussian errors too strong? I reckon they are doing significant work, as both the quadratic-form distributions used for certification and the independence between residual information and coefficient estimation are given by them. In fact, heteroskedasticity is common in real regression problems, so the strongest theoretical claim in this paper is inapplicable in not a few cases without further analysis. The authors should carefully consider this point.
  • When the noise variance is unknown, the procedure requires different certification and inference. It is shown that this is obtained through two independent banks of pure error. The experiments show that small banks may leave almost no groups with enough statistical power to even be considered. Sadly, this weakens practical applicability, as the method can require substantially more measurements than the regression dataset itself.
  • The adequacy margins, τH\tau_H and τA\tau_A are important because they determine what "good enough" means. However, the main experiments just use values such as 0.750.75 mainly as they make a useful benchmark. In my opinion, this choice of margins should be worked on more.
  • I understand that the authors extensively utilize ChatGPT for things like wording or sentence drafting, and have stated so in their AI-use statement. However, I still think that there is much room for improvement in how the idea can be conveyed through a manuscript. For example, try not to include too many sentences in the form of "This is an apple, not a pineapple."
  • Minor issue: the n−1/4n^{-1/4} rate in Corollary 19 is correct (according to my understanding). Calling it an incorrect rate might overstate the problem.
Questions for authors

I would highly appreciate it if the authors could provide the answers to these questions below:

  • When does the two-part check provide a meaningful practical advantage over the simpler pooled check? Can there be a scientifically motivated setting where checking disagreement between local affine models separately leads to significantly more useful report ? Moreover, how should one choose scientifically meaningful adequacy margins ?
  • Which realistic measurement setting can satisfy the assumptions and produce useful coefficient reports?
  • Does the precision advantage remain even when the splitting baseline can optimize its measurement allocation? Can the authors compare against a splitting procedure that chooses, before observing responses, how many repeated measurements to allocate to checking and coefficient estimation?
  • How sensitive are the guarantees to violations of the noise assumptions? Even addressing modest violations would help a lot.
  • How should the cells be chosen, and how sensitive are the conclusions to that choice? It would be great if the authors can show reporting sensitivity across several cell constructions, keeping the margins and error budgets fixed. This would clarify whether the reported conclusions are stable.
Reviewer_2YqsOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

The paper proposes elevating the coefficient reporting of local affine models into a statistical reporting contract with rigorous error guarantees.

Critical strengths

This is a theoretically sound work with extensive experiments. It clearly illustrates that good local model fitting does not imply that local affine coefficients are reportable.

Critical weaknesses

I am not deeply familiar with this research area. From my current perspective, the paper lacks experiments on real-world datasets and sufficient comparisons against baseline methods. The paper is quite lengthy and hard to follow.

Questions for authors

I believe the most critical revision is to better clarify the paper’s content and mathematical notations.

Reviewer_UzQsOpenReview ↗
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1
Confidence
2
Informativeness
2
Presentation
1
Soundness
3
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Paper summary

This paper is on certifying piecewise affine regression (PAR). Recall that typically in PAR, one first divides the data into some regions, and then produces an affine fit over data in each region. Now, within a region, one can have two types of errors: either the response is nonaffine, or the fit is bad (so that, e.g., the coefficients are wrong). The paper aims at the following problem: given a partitioning of the space into regions, and an audit dataset (X,Y)(X, Y), the paper will produce a certificate for each region, whereby the certificate both indicates that affineness over this region has not been rejected, and supplies a confidence interval.

Throughout, it is assumed that Y=μ+ε,Y = \mu + \varepsilon, where the latter term is noise, and the former is the mean at the corresponding XX. The noise is assumed to be Gaussian with variance σ2\sigma^2. Nevertheless, this σ2\sigma^2 is not assumed known: instead, the authors demand a "pure-error block", i.e., mm measurements of just the noise. Of course, if one has identical covariates, this can be achieved by taking a difference of the responses at these covariates. Under Gaussianity, the sample second moment of these error measurements gives an estimate of the noise variance with known distribution (χ2\chi^2). Validity of the procedure using this estimate relies on homoskedasticity, which is assumed.

High level, the proposed method goes as follows. Work in each region separately (I will drop region specific notation). Let NN be the number of points in the region. At first, divide the region into some JJ cells, where it is assumed that each cell has full-rank covariates. Note that the map from covariate to a prediction in linear regression is an operator that depends only on the covariates (namely, if the covariates are AA, then this map is P=A(A⊤A)−1A⊤P = A (A^\top A)^{-1} A^\top. Now, for each cell jj in this partition, produce this PjP_j, and stack them together into Π=diag(Pj)\Pi = diag(P_j). Alongside, compute a linear fit operator across the whole region, PP. Let HH denote the difference of these operators

First, the authors define a certain data-dependent hypothesis that they will test. This is such:

  1. For the true μ\mu, restricted to this region, ηH:=∣Hμ∣2σN≤τH.\eta_H := \frac{ \\| H \mu \\|_2 }{\sigma \sqrt{N} }\le \tau_H. In other words, the (normalised) difference in the per-cell and whole region fits is at most σ⋅τH\sigma \cdot \tau_H.
  2. For the true μ,\mu, restricted to this region, ηA:=∥(I−Π)μ∥2σN≤τA.\eta_A := \frac{ \| (I - \Pi) \mu\|_2}{\sigma \sqrt{N} } \le \tau_A. In other words, the normalised residual of the per-cell fit is ≤σ⋅τA\le \sigma \cdot \tau_A.

It is important to note that the authors don't tell us how to set τH,τA.\tau_H, \tau_A. Indeed, these values are assumed to be given to us. Notice also that this underlying noise-free hypothesis itself depends on the audit data.

Now, we only have access to noisy responses. To this end, the authors propose using FF-tests to check the hypothesis. Namely,

  1. Define FH=∣HY∣22/rS2,F_H = \frac{\\| HY \\|_2^2/r}{S^2}, where rr is the rank of HH. Notice that under Gaussianity of the noise, the numerator is a non-centred chi^2 random variable (with noncentrality growing with ηH2\eta_H^2), while the denominator is another chi^2 random variable computed from the pure error data (and so independent). The ratio thus is a non-centered F-random variable, with noncentering NηH2N \eta_H^2. The authors propose testing by thresholding this statistic at Fr,m,Nτ2−1(α/2M),F^{-1}_{r,m, N\tau^2}(\alpha/2M), which is standard in F-tests. Here α\alpha is the size of the overall procedure, and MM is the number of regions. 2M2M is thus the Bonferroni correction for 2 tests (see below) per region.

  2. Analogously, define FA=∣(I−Π)Y∣2/r′S2,F_A = \frac{\\| (I - \Pi) Y\\|_2/{r'}}{S^2}, where r′r' is the rank of (I−Π)(I-\Pi). Again, the same setup arises, and a F-test is proposed. Note that this component is very strongly reminscent of F-tests for linearity which rely on comparing the residual to a pure noise error, the difference here being that this is the residual of a per-cell fit rather than a fit over the whole region.

If both tests pass, then this region is "released," with the Bonferroni correction above accounting for working over the regions separately. The authors also mention that one can choose the worst-case p-value for these statistics to do a multiple-testing style release. For released regions, standard confidence intervals are fit around the point estimates, with variance estimated from a fresh batch of pure-error samples, and with confidence level inflated to ensure an overall FWER control on the released regions. It is emphasized that these may use the same response values as used in the above process.

It is shown that under this rule the size and validity is maintained, and that further that if both these tests pass, then the standard F-test of comparing residual over the whole region to the pure-error scale also passes (with appropriate threshold). It is also noted that power analysis and validity checks depends only on the projection operators HH, and so can be performed without looking at the audit responses (only covariates are needed).

Finally, simulations illustrating the behaviour of this and related methods are shown.

It is worth it to take a little stock of what is methodologically proposed here. Individual regions are treated separately, and each runs a certain test for affineness. These are integrated through standard methods to produce an overall decision as to which regions are certified or not, and standard confidence intervals for these are given. The key technical novelty, thus, is this test for affineness. Of course, ensuing results on its validity are new, although the approach is standard.

Critical strengths

The topic is certainly pertinent to ML venues. The setting assumed is somewhat limited (exact Gaussian noise, access to paired responses with the same mean, fixed router), but nevertheless the problem is of interest even given these restrictions. In its technical core, the affineness test is interesting---it is quite natural to move beyond the standard residual-based F-test, and the proposed way of setting up the underlying hypotheses is a reasonable way to do this (although see below). The validity analysis is well appreciated, albeit it would have been good to have power analysis accompanying it. To my reading, the results are correct, although I have only skimmed the proofs.

Critical weaknesses

Since this section is long, I will give a summary and my overall opinion before it. My first, and most important criticism, is to do with writing of the paper, which is very very unclear. My other two critiques are more technical. The first is to do with evaluation, for which I point out that an accounting of the distribution of (ηH,ηA)(\eta_H, \eta_A) studied is crucial to get pertinence. Finally, I talk a bit about the fact that the underlying hypothesis depends not only on the data (which is perhaps okay), but also on the pre-described cell paritioning of each region, which is a bit excessive.

My overall recommendation below, however, is mostly to do with the writing. This is so unclear and obfuscated that it is very hard, in my opinion, to usefully read this paper. The exposition is clearly well below the standards of any reasonable venue, and naturally, fixing this would require rewriting large parts of the paper, which cannot be accommodated into a conference review cycle. Thus, in my opinion, the paper is simply not ready, and needs more expository work before it's technical merits can even come to be considered.


On the writing. The writing of this paper is abysmal. Throughout, terminology is used without being defined, symbols appear out of nowhere, and language is needlessly dense and technical. One is left equal parts reeling, and trying to piece together scattered clues to figure out just what on earth the authors mean.

In fact, the writing is so poor that it is not even made clear that the main technical contribution is a new test for affineness. Instead, all this is dressed up amidst trivialities to do with Bonferroni corrections. I can hardly understand why an interesting contribution like that would be suppressed.

Of course, the main problem is not style, it is clarity. As a particularly striking example of the lack of clarity, even the the "problem setting" section is unclear! I have been reviewing ML conference papers since 2018, and reading for even longer. I have also written and reviewed statistics papers before. This is the first paper I have come across where unintroduced terminology and notation is used in the section whose typical purpose is to introduce terminology and notation!! How can this even happen?

All of this continues throughout the paper. The most egregious, perhaps, is the experiments section. Here, the baselines are not clearly specified, and their choice is not described. The actual details of experimental instances (how exactly the regression function μ\mu is picked) is not described, nor are we told how (ηH,ηA)(\eta_H, \eta_A) varied (or if they even are varied, rather than varying the thresholds). Further, trying to figure these things out in the appendix is even not easy. It took me a cool 20 minutes of scanning through pages upon pages before I found a definition of "NR" in a discussion in section E.9, and even this is stated inline. In any case, given the quality of the writing, I exercised my prerogative to not read the appendix to the largest extent my conscience would allow me.

Please please please note that it is NOT a readers job to intuit meaning and decipher clues. It is the authors' job to make sure that these things are clearly stated.

Let me give an example to justify this opinion, and why not just the problem setting section above.

  • 152-161: The very first paragraph already leaves me lost.

    • I don't understand what the pre-response design information is. Laws of the covariates? Something else?
    • What are response-free design screens, and what are power screens?
    • What are these prespecified certification rules, what are "requested coefficients"
    • What does it mean for something to "freeze independently of audit responses and scale measurements?" While I am at it, I guess audit responses are the YRY_R, but what are scale measurements?
    • What are transductive partitions? What are stable ID maps?

    It feels here that certain basic notations and terminology was just not set up. This immediately makes everything following confusing: now we are building upon this terminology that I don't know. So now I get the singular displeasure of trying to ferret out the meaning of all these terms from various context clues in the text. Why do this to your readers? Please be kinder to us.

    Anyway, my understanding is as follows, and I will judge the correctness on the basis of this. If my understanding is wrong, well, not my fault that things were not explained well enough.

    • there is a prespecified partition, as captured by rr, and audit data is assigned to these, for some reason calling these slots. These slots may or may not be audited, depending on certain somewhat mysterious criteria---this is the so-called screen. All this filtering can be done without seeing YR,Y_R, and this value is used only for slots which pass. "Releasing" is something that the auditor will do, whereby a linear fit over this region (on the basis only of the audit data, or some other linear fit given a priori?) will be made public. The problem is to decide what to release.
    • Even this basic thing: that the auditor 'releases' slots, is not stated. Not to mention the various other terms used for this in the paper, again without telling the reader. How am I supposed to dream up what "gating" means, for instance?
  • 162-168: I don't know what raw units are. It also seems needlessly complicated to set up things in terms of XX and ZZ in this way, especially since this is basically never used in the main text...

  • Lines 169-183:

    • I don't know what a completed discovery object is. SC,SIS_C, S_I are used before they are defined. The term "pure-error bank" is used as if it has already been defined (cue me searching the previous text and getting nada). Yb,r+Y_{b,r}^+ and Yb,r−Y_{b,r}^- are never defined.
    • What does it mean to "open after something freezes"? What does it mean to require independence and not just delayed opening? I have never come across "opening" in this context (also freezing might be overused).
    • This is hardly complicated stuff, btw. If you tell someone what is going on here in straightforward terms, this paragraph is a triviality to someone with statistical training. Consider this explanation: our procedure extends to unknown noise variance given pure-error samples. We thus assume access to mC+mIm_C + m_I samples drawn from the noise distribution. These may be realised by observing this many paired responses Y+,Y−Y^+, Y^- with matching means. (If space is available, one should add a comment about this being standard in F-tests here). This results in a sample variance estimates SC,SIS_C, S_I thus (3). These two variances are independent, which our analysis exploits, and used in different parts of the procedure: SCS_C to certify slots, and SIS_I to construct intervals. We let F0\mathcal{F}_0 denote the 'response-free' sigma-algebra over all aspects of the data and setting above, including covariates, router, slots et c., barring (Y,SC,SI)(Y, S_C, S_I).

On evaluation, and the comparison to NR. As mentioned above, in my opinion the key contribution is the affineness test of section 4.2. It is clear that this can be strung together with corrections into a procedure over the whole domain. The most natural question I had when turning to the experiments, thus, was how does this compare with using the standard F-test, aka NR in the paper.

While I mentioned the lack of clarity in the experimental section above, I have comments about the overall impression conveyed by this section, namely that NR is more conservative. I think that in order for me to accept this, the experiment design has to be particularly robust. The main issue is this: consider first N→∞N \to \infty, and imagine the performance of these two tests (the proposed C and NR) in the 2D space spanned by choices of (ηH,ηA)(\eta_H, \eta_A) as considered in the paper. Naturally, sets where the acceptance (or "release" or "report" or whatever) rate goes to 11 in this space are boxes for C and quarter-discs for NR. But note that this immediately means that if NR is tuned to reject all cases wherein either one of (ηH,ηA)(\eta_H, \eta_A) is larger than some threshold, it would leave a corner of the box uncovered (the disc would have to be tangent to the box, assuming even that the thresholds for the two are the same). In general, one could deviate from this somewhat, but nevertheless to get roughly similar size control over a certain region, NR would end up rejecting close to a corner point of a box where C accepts (I believe Prop 34 is essentially making this point). Of course, conversely, if the goal was to test if the residual energy relative to the affine fit were large, then the C test would have a mismatched acceptance region. In finite samples, this limiting behaviour manifests in two ways: both this high/low behaviour itself, and also in the shape of the rate curve as one explores various directions in the (ηH,ηA)(\eta_H, \eta_A) space (so, how far below 11 you are may depend on (ηH,ηA)(\eta_H, \eta_A) nonuniformly).

If we consider what we want in practice, neither of these hypotheses (box constraints on (ηH,ηA)(\eta_H, \eta_A) or ellipsoidal constraints) quite captures things in general: it depends on the application. I think, thus, to make a convincing case, one would either identify situations in which this box type thresholds on these two deviations are intrinsically preferable (this would carve out at least a niche where you should ideally use C), or one would evaluate at (ηH,ηA)(\eta_H, \eta_A) (or ideally on distributions over these) that favour both methods equally in some sense. Like, even if the goal was to sell C as a method over NR, I think a more convincing result would be something like showing that the loss of C relative to NR in situations that favour the latter is smaller than the loss of NR relative to C in situations which favour it. This would make C a good choice in absence of other information about the structure of how deviations from affineness arise. Functionally, this just requires a deeper scan over this parameter space, but with judicisouly chosen points. For instance, looking at table E.10, I found myself naturally wondering what happens at (0.28,0)(0.28,0) and (0,0.28).(0,0.28).


On the hypotheses. Given the context from the standard F-test, the use of a design-dependent hypothesis is okay. However, one thing that gives me pause is that the hypotheses in section 4.2 depend also on the cell partitions---as a result, the structure proposed ends up depending signficantly on an auxiliary detail. This might matter a fair deal, because in a sense the quality of the cells picked captures some sort of tradeoff between the two (ηH,ηA)(\eta_H, \eta_A) terms---as an example, if I pick the "right" cells, then the residual may collapse, but ηH\eta_H blow up, while if I pick two crude or misaligned cells, ηA\eta_A would increase while ηH\eta_H drops. Similarly, if I use more or fewer cells. I think I would find the results more convincing if either some notion of stability to the choice of this cell subdivision was developed. Is there a sense in which this can be given---if the cells are rich enough, et c.? Or alternatively, what happens if one averages over a few choices of these cells?

Questions for authors

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