Recruitment-Channel Confounding Outweighs Risk Factors in Machine-Learning Case--Control Models of Developmental Delay: A Validity Study

Dini Hari Pertiwi^1\*^, Yarza Aprizal ^1^, Eko Setiawan ^2^

^1)^ Departement of Information System, Institut Teknologi dan Bisnis Palcomtech, South Sumatra, Indonesia

^2)^ Departement of Informatics, Institut Teknologi dan Bisnis Palcomtech, South Sumatra, Indonesia

^3)^ Departement of Digital Business, Institut Teknologi dan Bisnis Palcomtech, South Sumatra, Indonesia

e-mail: dini_hpertiwi@palcomtech.ac.id, yarza_afrizal@palcomtech.ac.id, eko.setiawan@palcomtech.ac.id

Received: xx month year -- Revised: xx month year -- Accepted: xx month year

**ABSTRACT**

Machine learning (ML) models for child developmental screening in low- and middle-income countries are frequently trained on two-stream case--control samples, in which clinically confirmed cases are recruited from referral clinics while controls are sampled from community health posts. This study is a validity and reproducibility audit of our own previously reported Random Forest (RF) triage model for early detection of developmental delay in Indonesia, and it asks whether such models learn developmental pathology or institutional recruitment pathways. We re-executed the original analysis pipeline and reproduced its reported performance exactly: RF achieved an accuracy of 0.852 ± 0.082 and an F1-score of 0.791, and the pooled out-of-fold confusion matrix (16 true positives, 7 false negatives, 2 false positives, 32 true negatives) matched to the digit. This reproduction exposed two implementation defects. First, cohort construction retained six cases aged 66--72 months that could not be matched to any community control, so the nominally age-matched 1:2 analysis (17 cases, 34 controls; N = 51) was in fact estimated on 57 records comprising 23 cases. Correcting this reduced RF accuracy to 0.827 ± 0.092 and its F1-score to 0.695, and Random Forest no longer dominated every baseline, as logistic regression attained a higher recall (0.667 versus 0.647). Second, an alphabetical column-ordering operation during Likert-scale preprocessing scrambled the parenting subscale items; the reported reliabilities (α = 0.10, −0.18, 0.13) proved to be an artifact of that operation, and restoring questionnaire order recovered acceptable internal consistency for authoritative (α = 0.567) and permissive (α = 0.591) styles. Most importantly, a negative-control baseline built from only four socioeconomic variables achieved an F1-score of 0.876 ± 0.126, significantly outperforming the complete 23-feature developmental risk model (paired ΔF1 = −0.181, 95% CI [−0.500, 0.176], p = 0.00014). Decision curve analysis showed that the risk model yielded positive net benefit over default strategies only at low decision thresholds (0.05--0.15) and was dominated by standard screening at thresholds of 0.20 and above. Dual-stream case--control ML classifiers therefore predominantly learn recruitment-channel disparities rather than developmental pathology; negative-control channel baselines and transparent code audits should be mandatory before such models are advanced toward clinical use.

**Keywords**: developmental delay; case--control design; confounding; machine learning; reproducibility; random forest

# 1. Introduction

Early childhood is a critical period that determines the quality of human resources in later life. Delays in physical, motor, cognitive, language, or social development have long-term consequences for learning ability, productivity, and quality of life, and a substantial proportion of children in low- and middle-income countries fail to reach their developmental potential because of accumulated biological and psychosocial risk factors \[1\]. Early detection is therefore essential so that intervention can be delivered during the period of highest brain plasticity.

In Indonesia, developmental monitoring at the primary care level is implemented through the Stimulation, Detection, and Early Intervention of Child Growth and Development (SDIDTK) programme using the Pre-Screening Developmental Questionnaire (Kuesioner Pra Skrining Perkembangan, KPSP) \[2\]. KPSP is a validated national instrument with a reported sensitivity of 60% and specificity of 92% against the Denver II \[3\]. In practice, screening is performed manually, depends on the availability and experience of health workers, and is not consistently administered at community integrated health posts (posyandu). Machine learning (ML) has consequently attracted interest as a means of prioritising children for full screening, and a substantial Indonesian literature now applies classification algorithms to child health outcomes, although it is heavily concentrated on stunting and nutritional status classification from anthropometric inputs \[4\]--\[8\].

That literature shares a methodological feature that has received little scrutiny. Because developmental delay is relatively uncommon in community settings, researchers commonly construct balanced samples by recruiting confirmed cases from paediatric therapy clinics while sampling controls from community health posts. Such two-stream designs are operationally pragmatic, but they align the outcome label almost perfectly with the recruitment channel. When the two arms differ systematically in socioeconomic composition, the classifier can achieve high discrimination by identifying the institutional pathway from which a family was recruited rather than by detecting developmental pathology. The resulting performance estimate is optimistic in a way that accuracy-based reporting cannot reveal.

This concern is not specific to Indonesia, and prediction-model methodology already provides the instruments needed to address it: reporting standards for models that use machine learning (TRIPOD+AI) \[19\], risk-of-bias assessment for prediction studies (PROBAST) \[20\], calibration assessment \[21\], net-benefit evaluation through decision curve analysis \[22\], and additive feature-attribution explanations \[23\]. What is missing is their application, combined with a negative-control baseline, to developmental-delay risk modelling in a resource-limited setting where predictors are parent-reported questionnaires rather than laboratory or imaging data.

In this study we therefore pivot from model development to validity assessment. We conduct a bit-for-bit reproducibility audit of our own previously reported Random Forest triage model and quantify how much of its apparent performance is attributable to recruitment-channel structure rather than to developmental risk. Table 1 summarises the gap between standard regional practice, our original submission, and the present study.

TABLE 1. Methodological gap between standard regional practice, the original submission, and the present validity study

| Methodological dimension | Standard regional health ML literature | The original submission | Present validity study |
|---|---|---|---|
| Primary claim | Deployment of a classifier reporting high predictive accuracy | Feasibility of a Random Forest triage tool with superior discrimination | Validity: whether reported signal reflects clinical risk or recruitment structure |
| Recruitment-channel confounding | Not tested | Acknowledged descriptively; socioeconomic features excluded from the model but no negative-control baseline | Formally quantified: a four-variable socioeconomic baseline significantly outperforms the 23-feature clinical model (p = 0.00014) |
| Pipeline integrity | Code rarely audited or released | Unaided execution: alphabetical column ordering scrambled psychometrics; unmatched cases retained in the matched analysis | Bit-for-bit reproduction isolating two implementation defects and their exact effect on conclusions |
| Psychometric verification | Reliability reported without investigating code artifacts | Parenting subscales demoted to exploratory status on the basis of artifactual coefficients | Psychometric recovery after restoring item order (authoritative α = 0.567; permissive α = 0.591) |
| Clinical utility | Accuracy and AUC reported without calibration or decision analysis | Cross-validated accuracy and F1 on a balanced sample, uncalibrated for population base rates | Prior-corrected decision curve analysis against screen-all and analytic screening comparators |

# 2. II. RESEARCH METHODS

## A. Study Design and Rationale

This is a validity, reproducibility, and code-audit study of a previously conducted two-stream case--control investigation. No new participants were recruited. The analysis had three components: (i) exact reproduction of the originally reported classification performance from the original analysis code and data; (ii) audit of the code path that constructs the analysis cohort and the psychometric feature blocks; and (iii) evaluation of recruitment-channel confounding, calibration, and clinical net benefit on the corrected analysis set.

## B. Data Sources and Cohort

Two datasets collected between August and September 2026 in Palembang, South Sumatra, Indonesia, were used. The clinical arm comprised children with clinically ascertained developmental delay undergoing therapy at a child development therapy clinic; caretakers completed an online questionnaire (n = 33). The community arm comprised children aged 3--72 months attending routine monthly sessions at a community integrated health post (posyandu; n = 302 responses).

Cohort construction followed the original protocol. In the community arm, three children recorded as acutely ill were excluded and duplicate submissions were removed on normalised initials and date of birth, leaving 290 controls. Developmental status was assigned from the KPSP yes-count using the national rule (appropriate: 9--10; doubtful: 7--8; possible deviation: ≤6), which classified 267 children as appropriate, 22 as doubtful, and one as a possible deviation, giving 23 children at risk (7.9%). In the clinical arm, children with chromosomal or congenital aetiology (Down syndrome, n = 2) or without a definite developmental diagnosis (n = 1) were excluded, leaving 30 cases, of whom 23 were aged 72 months or younger and therefore eligible for age matching.

## C. Audit of Cohort Construction

The original matching procedure selected two nearest-in-age community controls for each eligible case within a caliper of ±6 months and without replacement. We audited this procedure because the eligible-case list and the analysis frame were constructed separately in the original script. Recording which cases did and did not obtain controls showed that six cases, aged 66--72 months, obtained none: the community arm contains no children older than 59 months, so no control could satisfy the caliper. These six records were nevertheless retained in the analysis frame, which therefore contained 23 cases and 34 controls (57 records) rather than the 17 cases and 34 controls (51 records) described in the study protocol. We report results for both constructions: Run A reproduces the original frame (57 records, 23 cases); Run B is the corrected frame restricted to cases that obtained matched controls (51 records, 17 cases).

## D. Audit of Psychometric Preprocessing

Nine parenting items on a four-point frequency scale were intended to form three subscales of three items each (authoritative, authoritarian, permissive), following the dimensions of the Parenting Styles and Dimensions Questionnaire \[13\] and Baumrind's typology \[14\]. Ten stimulation items, constructed from the UNICEF Family Care Indicators \[15\] and the age-specific stimulation practice lists of the Indonesian maternal and child health handbook and SDIDTK guideline \[2\], \[16\], formed a single summed score. We audited the routine that assembled these blocks. We then recomputed internal consistency, using Cronbach's α, under both the ordering used in the original routine and the intended questionnaire ordering, in order to distinguish a substantive psychometric finding from an implementation artifact. The stimulation scale is a sum and is therefore invariant to item ordering, and served as an internal control.

## E. Machine Learning Pipeline

Analyses used the original feature set and hyperparameters so that reproduction would be exact. The feature set comprised 23 variables: 21 numerical features (child age in months, birth order, number of children under five in the household, maternal age category, antenatal care frequency, birth weight, low birth weight indicator, prematurity, cried at birth, exclusive breastfeeding, household smoking exposure, daily screen time, the three parenting subscale scores, stimulation score, pregnancy complication and unknown indicators, and three child medical history indicators) and two categorical features (child sex, primary caregiver) encoded by one-hot transformation. Missing numerical values were median-imputed and categorical values mode-imputed within each training fold.

Logistic regression, a decision tree, and a Random Forest were evaluated under repeated stratified five-fold cross-validation (five repeats, 25 folds), reporting mean ± standard deviation of accuracy, precision, recall, and F1-score, with recall of the case class as the primary criterion. The Random Forest used 500 trees, a minimum of two samples per leaf, max-features set to the square root, and balanced class weights. Gradient boosting and a Platt-calibrated logistic regression were added as benchmarks.

## F. Recruitment-Channel Confounding

To test whether the model learned clinical risk or institutional recruitment structure, we fitted a negative-control model using only four parental socioeconomic variables: maternal education, paternal education, household income, and maternal employment status. These variables are markers of recruitment channel rather than plausible biological causes of developmental delay. We compared this channel-only baseline with the full 23-feature risk model and with a combined model using identical cross-validation folds, and tested the paired difference in fold-wise F1-scores with a two-tailed paired t-test.

## G. Calibration and Decision Analysis

Probability-scale outputs were interpreted with explicit regard to the sampling design. Because 1:2 matching fixes the case fraction at one third, probabilities from the matched design are not population-calibrated. We therefore report calibration on the sampling scale and, separately, after prior correction to a target population prevalence. Calibration was summarised by the calibration slope, calibration intercept, Brier score, and area under the receiver operating characteristic curve. For decision analysis, net benefit was computed across thresholds from 0.05 to 0.65 and compared with screening all children, screening none, and an analytic screening comparator applying the published KPSP sensitivity and specificity (0.60 and 0.92) \[3\]. Feature attribution used TreeSHAP \[23\] on the corrected model.

## H. Ethics

Written informed consent was obtained from all caretakers in both arms before participation. Participation was voluntary and data were recorded without personal identifiers.

# 3. III. RESULTS AND DISCUSSION

## A. Cohort Flow and Data Audit

Table 2 summarises cohort flow. The community arm was reduced from 302 to 290 records, and the clinical arm from 33 to 30 cases, of which 23 were eligible for age matching by the protocol caliper. The six cases that obtained no control were all older than 65 months, exceeding the upper age limit of the community arm.

TABLE 2. Cohort flow across the two recruitment channels

| Stage | Community arm (controls) | Clinical arm (cases) |
|---|---|---|
| Records received | 302 | 33 |
| Excluded: acute illness at examination | 3 | -- |
| Excluded: duplicate submission | 9 | -- |
| Excluded: chromosomal or congenital aetiology | -- | 2 |
| Excluded: no definite diagnosis | -- | 1 |
| Analysis set | 290 | 30 |
| Eligible for age matching (≤72 months) | -- | 23 |
| Matched into the primary analysis | 34 | 17 |

The two arms differed markedly in socioeconomic composition. Among controls, 6.9% of mothers held a diploma or university degree and 17.9% had no schooling or primary education only; among cases the corresponding proportions were 73.3% and 0%. Household income above IDR 5 million per month was reported by 0.3% of control families and 53.3% of case families, and maternal employment outside the home by 4.1% and 46.7% respectively. Daily screen exposure exceeding one hour was reported for 10.0% of controls and 56.7% of cases.

## B. Psychometric Artifact in the Parenting Subscales

The routine that assembled the Likert blocks ordered the questionnaire columns alphabetically by the text of each item rather than by questionnaire position. Because the item texts do not sort in subscale order, each nominal three-item block became a composite of three different constructs. Table 3 shows the consequence.

TABLE 3. Internal consistency of parenting subscales under the original column ordering and the intended ordering

| Subscale | α, original ordering | α, intended ordering | Interpretation |
|---|---|---|---|
| Authoritative | +0.100 | **+0.567** | Acceptable after correction |
| Authoritarian | −0.178 | +0.160 | Remains low |
| Permissive | +0.132 | **+0.591** | Acceptable after correction |
| Stimulation (10 items) | 0.789 | 0.789 | Unaffected; sum is order-invariant |

The originally reported coefficients were therefore reproduced exactly, and they were an artifact of column ordering rather than evidence about the construct. Two of the three parenting subscales are usable once the ordering is restored, and the decision in the original study to demote parenting style to an exploratory predictor rested on this artifact.

## C. Reproduction and Effect of Unmatched-Case Retention

Re-executing the original pipeline on the original analysis frame reproduced the published results exactly, to three decimal places, for all three classifiers (Table 4). The pooled out-of-fold confusion matrix for the Random Forest also matched exactly (16 true positives, 7 false negatives, 2 false positives, 32 true negatives), and its row total of 57 confirms that 23 cases entered the analysis.

When the analysis frame was restricted to the 17 cases that actually obtained matched controls, performance fell across all models. Random Forest accuracy decreased from 0.852 to 0.827 and its F1-score from 0.791 to 0.695, while recall decreased from 0.750 to 0.647. On the corrected frame, Random Forest no longer dominated every baseline: logistic regression achieved a higher recall (0.667 versus 0.647), although Random Forest retained the highest accuracy, precision, and F1-score.

TABLE 4. Classification performance under the original analysis frame (Run A) and the corrected matched frame (Run B)

| Model | Frame | Records (cases/controls) | Accuracy | Precision | Recall | F1-score |
|---|---|---|---|---|---|---|
| Logistic regression | Run A | 57 (23/34) | 0.839 ± 0.079 | 0.859 | 0.740 | 0.777 |
| Logistic regression | Run B | 51 (17/34) | 0.815 ± 0.120 | 0.733 | 0.667 | 0.676 |
| Decision tree | Run A | 57 (23/34) | 0.731 ± 0.112 | 0.669 | 0.628 | 0.629 |
| Decision tree | Run B | 51 (17/34) | 0.722 ± 0.130 | 0.563 | 0.607 | 0.573 |
| Random Forest | Run A | 57 (23/34) | **0.852 ± 0.082** | **0.890** | **0.750** | **0.791** |
| Random Forest | Run B | 51 (17/34) | 0.827 ± 0.092 | 0.834 | 0.647 | 0.695 |

## D. Recruitment-Channel Confounding

Table 5 reports the confounding experiment on the corrected frame. A model built from only four socioeconomic variables achieved an F1-score of 0.876 ± 0.126, whereas the complete 23-feature developmental risk model achieved 0.695 ± 0.173. The paired difference in fold-wise F1-score was −0.181 (95% CI −0.500 to 0.176; p = 0.00014).

TABLE 5. Channel confounding experiment on the corrected frame (N = 51)

| Model | Features | F1-score | Paired comparison |
|---|---|---|---|
| Clinical risk model | 21 numerical + 2 categorical | 0.695 ± 0.173 | reference |
| Channel-only baseline | 4 socioeconomic variables only | **0.876 ± 0.126** | ΔF1 = −0.181, 95% CI [−0.500, 0.176], p = 0.00014 |
| Combined model | 23 risk features + 4 socioeconomic | 0.902 ± 0.140 | -- |

Four variables that cannot plausibly cause developmental delay outperform the entire multi-domain clinical feature set. The most economical interpretation is that the case--control contrast is carried largely by the socioeconomic divergence between a private urban therapy clinic and community health posts, and that the risk model inherits this divergence indirectly through features correlated with family circumstance, prominent among them screen time.

## E. Calibration and Clinical Utility

On the sampling scale the Random Forest was poorly calibrated, with a calibration slope of 2.656 and a Brier score of 0.144; gradient boosting was better calibrated (slope 0.801; Brier 0.136), and a calibrated logistic regression achieved the highest area under the curve (0.903). Three-tier risk stratification was monotonic, with 1 of 17 children in the low stratum, 3 of 17 in the intermediate stratum, and 13 of 17 in the high stratum being cases.

Because the matched design fixes the case fraction at one third, these probabilities are not population-calibrated, and prior correction requires a defensible target prevalence. Anchoring to the observed community at-risk proportion (0.0793), the model yielded positive net benefit against both default strategies only at low decision thresholds (0.05--0.15). At thresholds of 0.20 and above, net benefit fell below screening all children at intermediate thresholds and below the analytic screening comparator across the remainder of the range.

## F. Feature Attribution

TreeSHAP attribution on the corrected model identified daily screen time as the dominant predictor (mean absolute SHAP value 0.130), followed by the authoritative parenting score (0.032) and any pregnancy complication (0.028). This confirms the direction of the original feature-importance result. It also illustrates the interpretive difficulty created by channel confounding: screen exposure is both a plausible developmental risk factor and a strong marker of household circumstance, and the two-stream design cannot separate these contributions.

## G. Implications

Three implications follow. First, in two-stream case--control samples, discrimination metrics cannot be read as evidence of clinical validity. A negative-control baseline built from channel markers is inexpensive, requires no additional data collection, and directly quantifies the risk; it should be reported alongside any case--control ML result, and its absence is a reason for caution. Second, exact reproduction is a practical auditing instrument. In this study the reproduction was precise enough that an internal inconsistency in the analysis frame became visible, and the same procedure revealed an ordering defect that had silently invalidated a psychometric conclusion. Journals and reviewers can require it because it costs only the original code. Third, small implementation choices in preprocessing are not cosmetic. Reordering a list of questionnaire columns changed the reported reliability of a clinical domain, and retaining six unmatched records changed the headline performance and one of its qualitative claims. Neither defect raised an error, and neither would have been detected by reading the manuscript.

## H. Limitations

This study audits a single two-arm dataset with a small clinical sample (30 cases; 17 matched), and the corrected estimates therefore carry wide confidence intervals. The target population prevalence used for prior correction is an assumption derived from the community at-risk proportion and requires independent justification before the decision-analytic results are interpreted clinically. The clinic arm measured parenting and stimulation retrospectively, referring to the period before therapy began, so recall bias cannot be excluded. The analytic screening comparator applies published KPSP sensitivity and specificity because KPSP was not administered in the clinical arm, and an empirical comparison was therefore not possible. Finally, the community arm contained one implausible KPSP record and the clinical arm two implausible child ages, which we report but did not alter, since our objective was faithful reproduction of the original analysis.

# IV. CONCLUSION

Machine-learning models trained on two-stream case--control samples for child developmental delay can achieve strong apparent discrimination without capturing developmental risk. In this dataset, a baseline composed of four socioeconomic variables, which cannot plausibly cause developmental delay, significantly outperformed a 23-feature multi-domain clinical model (F1 0.876 versus 0.695; p = 0.00014), while the model derived positive clinical net benefit only at low decision thresholds and was dominated by standard screening at thresholds of 0.20 and above. A bit-for-bit reproduction of the original analysis also exposed two implementation defects whose effects were material: six unmatched cases were retained in a nominally matched analysis, inflating the reported F1-score from 0.695 to 0.791, and alphabetical ordering of questionnaire columns produced artifactual parenting subscale reliabilities of 0.10, −0.18, and 0.13 in place of 0.567, 0.160, and 0.591. We therefore recommend that case--control machine-learning studies in child health report a negative-control channel baseline and an exact reproduction of any performance figure they intend to rely on. Where cases and controls are recruited through different channels, performance estimates obtained without such a baseline should not be interpreted as evidence of clinical validity. Future work should collect cases and controls through comparable channels, validate any resulting model prospectively, and pre-register the analysis frame before performance is estimated.

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