# Reframed Framing Package — Jurnal ELTIKOM Resubmission

**Manuscript (working title):** Random Forest Classification for Early Detection of Developmental Delay Risk in Children Based on Parenting, Stimulation, and Perinatal Risk Factors
**Authors:** Dini Hari Pertiwi, Yarza Aprizal, Eko Setiawan (Institut Teknologi dan Bisnis Palcomtech, South Sumatra, Indonesia)
**Purpose of this file:** replace the manuscript's Title, Abstract, Introduction, Contributions, and Conclusion with a framing that states the contribution explicitly and maps each claim to a specific gap. All numbers are taken from `manuscript-v1.txt`; anything that would require a new analysis is written as `[[TO BE COMPUTED: ...]]`. No result, metric, or p-value is invented.

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## (a) Proposed Titles

**Option A — problem / triage-framed (recommended lead title)**

> **From Screening to Triage: An Interpretable Random Forest Model of Modifiable Caregiving and Perinatal Risk Factors for Early Detection of Developmental Delay in Indonesia**

*Rationale:* names the clinical decision problem (who gets screened first), states the input class (modifiable caregiving/perinatal factors, i.e. no test items), and states the deliverable (interpretable triage aid). It promises a decision tool, not another classifier.

**Option B — validity-forward**

> **Caregiving-Based Machine Learning Triage for Developmental Delay Risk: An Age-Matched Case–Control Study Quantifying Recruitment-Channel Confounding and Delimiting Risk Modelling from Formal Screening**

*Rationale:* foregrounds the two components that distinguish this study from the Indonesian stunting/nutrition machine-learning literature — explicit quantification and mitigation of recruitment-channel confounding (C2), and the negative boundary result that delimits what questionnaire risk models can replace (C4). Appropriate if the journal's reviewers weight internal validity and reporting standard over the clinical use case.

Both titles remain accurate to what the study actually did. Neither claims external validation, a new algorithm, or clinical effectiveness.

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## (b) Rewritten Abstract (~230 words)

**Abstract**

Developmental delay in early childhood has long-term consequences for learning, productivity, and quality of life, yet detection in Indonesia depends on manual, health-worker-intensive administration of the Pre-Screening Developmental Questionnaire (KPSP), a national instrument with a reported sensitivity of 60%. This study reframes machine learning for this problem as a **triage** task — prioritising children for full screening — rather than a replacement for screening, and reports the model as a clinical prediction model following TRIPOD+AI conventions [TRIPOD+AI; [[VERIFY CITE]]].

We developed and evaluated a Random Forest model to distinguish clinically ascertained developmental delay cases from community controls using exclusively questionnaire risk factors (demographics, perinatal history, parenting style, stimulation practices, and screen time); no developmental test items were used as features. Cases were 30 children undergoing therapy at a child development therapy clinic in Palembang; controls were 290 children attending a community integrated health post (posyandu). The primary analysis matched 17 cases with 34 controls on child age (±6 months, 1:2). Under repeated stratified five-fold cross-validation, Random Forest achieved accuracy 0.852 ± 0.082, precision 0.890 ± 0.129, recall 0.750 ± 0.198, and F1-score 0.791 ± 0.141, outperforming logistic regression and decision tree baselines. Permutation importance identified screen time as the dominant predictor, followed by child age, household smoking exposure, birth weight, child sex, and authoritative parenting.

Because cases and controls were recruited through different channels, we treat recruitment-channel confounding as a first-class validity question rather than a caveat: a channel-only baseline, socioeconomic matching, and a channel-invariance check are reported [[TO BE COMPUTED: channel-only baseline AUC/recall; SES-matched matched-set size and performance; within-channel feature-importance ordering]], alongside calibration [[TO BE COMPUTED: calibration slope, intercept, Brier score, calibration curve]] and decision-curve net benefit versus screen-all and KPSP-only strategies [[TO BE COMPUTED: net benefit at candidate thresholds]]. A secondary analysis found that the same questionnaire factors did not discriminate KPSP outcomes in the unselected community sample (recall of the at-risk class 0.15), formally delimiting the model's role: it prioritises children for full KPSP administration and referral, and does not substitute for it. Per-child SHAP explanations [[TO BE COMPUTED: SHAP values for a worked flagged-child vignette]] convert model output into counselling targets for frontline workers.

**Keywords:** developmental delay; clinical prediction model; random forest; triage; recruitment-channel confounding; decision curve analysis; screen time; KPSP

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## (c) Rewritten 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 through the accumulation of 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 primary care level is implemented through the SDIDTK programme using the Pre-Screening Developmental Questionnaire (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, however, screening is performed manually, depends on the availability and experience of health workers, and is not consistently administered at community integrated health posts (posyandu); children at risk are therefore frequently identified late, particularly where human resources are limited. A sensitivity of 60% means that two in five children with delay are missed by the instrument itself, independently of coverage.

Machine learning has been applied widely to child health classification in Indonesia, but that literature is heavily concentrated on stunting and nutritional status classification from anthropometric inputs [4]–[8]. Predicting developmental delay from modifiable caregiving and perinatal factors has received far less attention, and — importantly for a prediction-model paper — the existing work reports discrimination metrics only. It does not report calibration, does not translate model output into a decision rule with net benefit, and does not confront the confounding that arises when cases and controls are recruited through different channels.

That last point is a general methodological gap, not a local one. When cases are recruited from a therapy clinic and controls from a community post, a model can learn to separate *channels* rather than *outcomes*; the resulting performance estimate is optimistic unless the confound is quantified and, where possible, removed. Prediction-model methodology already provides the tools for this — risk-of-bias assessment [PROBAST; [[VERIFY CITE]]], reporting standards for models using machine learning [TRIPOD+AI; [[VERIFY CITE]]], calibration assessment [Van Calster et al., 2019; [[VERIFY CITE]]], net-benefit evaluation [Vickers & Elkin, 2006; [[VERIFY CITE]]], and additive feature-attribution explanations [Lundberg & Lee, 2017; [[VERIFY CITE]]]. What is missing is their application to developmental-delay risk modelling in a low- and middle-income country setting, where the available predictors are questionnaires administered by frontline workers rather than laboratory or imaging data.

At the same time, the developmental science literature consistently identifies caregiving factors — responsive parenting, home stimulation, and, more recently, screen time exposure — as modifiable predictors of early developmental outcomes [1], [10], [11], [12]. A prediction model built on such factors is actionable in a way that a model built on fixed perinatal characteristics is not: parenting, stimulation, and screen exposure can be targeted by counselling at primary care level.

**Gap statement.** Table G sets out what each strand of prior work established and, specifically, what it leaves unaddressed. Each row maps to one of the contributions stated in Section (d).

**Table G. What prior work addressed and what remains unaddressed**

| Prior work | What it did | What it does NOT address |
|---|---|---|
| Walker et al., 2011 [1] | Synthesised epidemiological evidence on biological and psychosocial risk and protective factors for early child development in low- and middle-income countries | Provides associations, not a predictive model; no risk score, no stratification, no deployable triage rule |
| WHO/UNICEF/World Bank, 2018 [10] | Set out the Nurturing Care Framework, identifying responsive caregiving and stimulation as policy-level levers | Framework and policy guidance; no per-child risk estimation, no model development or validation |
| Kementerian Kesehatan RI, 2016 — SDIDTK [2] | Defined the national protocol for growth and development monitoring, including KPSP administration | Manual and health-worker-dependent; no prioritisation rule when screening capacity is short of demand |
| Dhamayanti, 2006 [3] | Validated KPSP against the Denver II (sensitivity 60%, specificity 92%) | Instrument validation only; leaves the 40% false-negative rate of the instrument itself unaddressed and offers no complementary risk model to prioritise administration |
| Madigan et al., 2019 [11] | Reported an association between screen time and lower developmental screening scores in a large cohort | Association, not prediction; no case–control model, no calibration, no decision rule, no triage pathway |
| Chonchaiya & Pruksananonda, 2008 [12] | Linked television viewing to delayed language development in a small clinical sample | Not a prediction model; a single exposure; sample too small to support risk stratification |
| Candra et al., 2024 [4] | Classified stunting from nutritional status using SVM | Anthropometric outcome, not developmental delay; no caregiving questionnaire predictors; accuracy-only reporting with no calibration or net benefit |
| Dhani et al., 2024 [5] | Improved stunting classification accuracy with Random Forest, ANOVA feature selection, and SMOTE | Same outcome mismatch; no decision framework; no treatment of confounding by recruitment or sample construction |
| Syahfitri et al., 2024 [6] | Compared machine learning algorithms for stunting prediction | Benchmark comparison only; no decision analysis; no developmental outcome |
| Lestari, 2024 [7] | Applied bagging and Random Forest to stunting prediction | Same as above; no caregiving or stimulation predictors |
| Ratnasari et al., 2024 [8] | Detected stunting early from anthropometric indicators using machine learning | Anthropometry-only inputs; cannot identify modifiable counselling targets; no calibration or net-benefit reporting |
| Breiman, 2001 [9] | Introduced Random Forest: bagged trees with random feature selection, plus out-of-bag importance | A method paper; it says nothing about validity under biased case–control sampling or about the clinical decision utility of its output |
| Robinson et al., 1995 [13]; Baumrind, 1971 [14] | Developed the Parenting Styles and Dimensions Questionnaire and the underlying parenting typology | Instrument and theory developed in Western samples; psychometric behaviour of short Indonesian adaptations is unreported, and these dimensions have not previously served as predictors in this population |
| Kariger et al., 2012 [15] | Developed the Family Care Indicators for use in multi-country surveys | A measurement instrument; provides no prediction, no threshold, and no triage logic |
| Kementerian Kesehatan RI — KIA handbook [16] | Defined age-specific stimulation practices and the maternal-child health record used at posyandu | Practice guidance and record-keeping; not a risk model, and not evaluated for predictive value |
| WHO, 2006 [17] | Published child growth standards for length/height-, weight- and BMI-for-age | Anthropometric reference only; nutritional status is not used as a model feature in the present study |
| Chawla et al., 2002 [18] | Introduced SMOTE for class-imbalanced learning | A resampling method; it redistributes class balance but does not address confounding by recruitment channel |
| Wolff et al., 2019 — PROBAST [Ann Intern Med 2019;170:51–58] | Provided a risk-of-bias and applicability assessment tool for prediction-model studies | A tool, not a study; the developmental-delay and Indonesian child-health machine-learning literature cited above largely does not apply it |
| Collins et al., 2024 — TRIPOD+AI [BMJ 2024;385:e078378] | Defined reporting standards for clinical prediction models, including machine-learning models | Standards, not evidence; prior work in this domain rarely reports calibration, net benefit, or sampling-related confounding in accordance with them |
| Vickers & Elkin, 2006 — decision curve analysis [Med Decis Making 2006;26:565–574] | Introduced net-benefit decision curves for evaluating prediction models | A method; absent from the stunting/nutrition machine-learning literature cited above, where accuracy remains the reported endpoint |
| Lundberg & Lee, 2017 — SHAP [NeurIPS 2017] | Introduced additive feature-attribution explanations for predictive models | A method; not yet used in this domain to derive per-child, actionable counselling targets for frontline workers |

This study therefore develops and evaluates a Random Forest model for triage of developmental delay risk. Random Forest aggregates many decision trees trained on bootstrap samples with random feature selection, giving robustness to non-linear relationships, mixed variable types, and class imbalance while producing feature-importance estimates usable by domain experts [9] — properties that suit heterogeneous, partly categorical community health questionnaire data. Following the gaps in Table G, the study is framed as a clinical prediction model rather than an algorithm comparison, and its contribution concerns the problem, the validity of the case–control contrast, the decision framework, an explicit boundary result, and per-child interpretability for counselling.

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## (d) Rewritten Contributions (5 falsifiable, gap-mapped claims)

Each claim below states what would falsify it, so a reviewer can test rather than accept it. Where a claim depends on analyses not yet present in `manuscript-v1.txt`, the required quantity is marked.

**C1 — Problem (falsifiable).**
To our knowledge, this is the first prediction model for early-childhood developmental delay in Indonesia built exclusively from caregiving, perinatal, and demographic risk factors, using no developmental test items as features, and delivered as an interpretable triage aid rather than a diagnostic classifier.
*Gap filled:* rows for [4]–[8] (Indonesian machine learning confined to stunting and nutritional status from anthropometry), [3] (KPSP validation without a complementary risk model), [2] (manual, capacity-limited national screening).
*Falsified by:* any published model for developmental-delay risk in Indonesian children using exclusively non-test questionnaire risk factors. The claim is deliberately scoped — "in Indonesia", "exclusively modifiable caregiving/perinatal factors" — and should be reported as "to our knowledge" rather than as an absolute priority claim.

**C2 — Validity (falsifiable).**
An age-matched case–control design contrasting clinically ascertained cases from a therapy clinic with community controls is combined with explicit *quantification and mitigation* of recruitment-channel confounding, rather than reporting it as a caveat. Specifically: (i) a channel-only baseline to show the risk factors add predictive value beyond recruitment channel; (ii) re-matching or residualisation on socioeconomic status in addition to age; and (iii) a channel-invariance check of feature-importance ordering (within-channel and under channel hold-out).

Quantities already available: adding socioeconomic features raised unmatched-sample Random Forest performance to accuracy 0.983 and F1 0.870, evidence that part of the case–control contrast is carried by channel-linked socioeconomic differences; these features are excluded from the primary model.
*Required additions:* `[[TO BE COMPUTED: channel-only baseline performance on the matched set; SES-matched matched-set size and primary metrics; within-channel permutation-importance ranking versus the pooled Table 3 ranking]]`
*Gap filled:* row for [18] and the [4]–[8] rows — resampling and accuracy-tuning do not address sample-construction confounding; Table G shows no prior row in this domain quantifies it.
*Falsified by:* a channel-only baseline that performs as well as the full risk-factor model (then the model adds no information beyond recruitment channel), or a SES-matched model whose performance collapses to chance (then the primary result is a SES artefact). Either outcome must be reported; the claim is that the confound is measured and bounded, not that the model is unaffected.

**C3 — Decision (falsifiable).**
Calibration and decision-curve net-benefit analysis, with a cost-sensitive threshold, convert the classifier into a specified component of a triage pathway relative to KPSP: the model's stated role is to rank children for full KPSP administration where coverage is constrained.
*Required additions:* `[[TO BE COMPUTED: calibration slope and intercept, Brier score, calibration curve on the held-out set; net benefit of the model versus screen-all and KPSP-only at a pre-specified threshold range; the chosen operating threshold and the resulting sensitivity/specificity trade-off]]`
*Existing anchors:* pooled out-of-fold predictions currently give 16 true positives, 7 false negatives, 2 false positives, and 32 true negatives (accuracy 0.842, sensitivity 0.696, specificity 0.941). A net-benefit analysis is required before this claim can be made; discrimination alone does not establish clinical utility.
*Gap filled:* Table G rows for Vickers & Elkin (decision curves absent from the domain literature) and the accuracy-only reporting in [4]–[8].
*Falsified by:* net benefit no greater than either comparator (screen-all or KPSP-only) across the plausible threshold range. Given 17 matched cases, calibration and net-benefit estimates will be imprecise and must be reported with confidence intervals; a null or narrow net-benefit result at realistic thresholds would falsify the triage claim and must be stated as such.

**C4 — Boundary (falsifiable).**
A negative secondary result formally delimits what questionnaire-based risk models can and cannot replace: the same questionnaire factors did not reproduce KPSP screening outcomes within the unselected community sample (recall of the at-risk class 0.15), whereas group comparisons within that sample showed that only birth weight differed between screening groups (median 2700 g versus 3000 g; p = 0.001), with parenting, stimulation, and screen time not differing.
*Gap filled:* no row in Table G reports this boundary; [11] and [12] establish association but not the limits of representation-based prediction, and [3] provides no complementary model at all.
*Falsified by:* re-analysis showing that questionnaire factors do reproduce KPSP outcomes in an unselected sample at operationally useful recall — which would extend, rather than refute, the model's scope.

**C5 — Interpretability (falsifiable).**
SHAP-based per-child explanations yield actionable counselling targets for frontline workers, supplementing (not replacing) global permutation importance.
*Existing anchors:* permutation importance on the holdout identified screen time as the dominant predictor (0.223 ± 0.083), followed by child age (0.162 ± 0.076), household smoking exposure (0.112 ± 0.065), birth weight (0.076 ± 0.052), child sex (0.066 ± 0.041), and authoritative parenting (0.043 ± 0.053).
*Required additions:* `[[TO BE COMPUTED: SHAP values for a worked flagged-child vignette; agreement between SHAP rank ordering and permutation-importance rank ordering across folds]]`
*Gap filled:* Table G row for Lundberg & Lee (SHAP not yet applied to per-child counselling targets in this domain); the [4]–[8] rows report at most global importances.
*Falsified by:* SHAP attributions that are unstable across folds or that contradict the permutation-importance ranking, which would make per-child counselling targets unreliable. Where SHAP points to screen time and household smoking, the counselling target is concrete; where it points to birth weight or child sex, no modifiable target exists and this must be stated plainly rather than presented as actionable.

**Honest scope note for all five claims.** Parenting subscale reliabilities were α = 0.10 (authoritative), −0.18 (authoritarian), and 0.13 (permissive); the stimulation scale was reliable (α = 0.789). Parenting is therefore presented as an exploratory predictor and is deliberately *not* used as a load-bearing element of any contribution claim. The matched primary sample is 17 cases and 34 controls; no contribution is claimed on the basis of performance magnitude, and all performance-dependent claims (C2, C3, C5) are stated as procedures to be reported, with falsification conditions, rather than as established results.

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## (e) Rewritten Conclusion

This study reframes machine learning for early detection of developmental delay in Indonesia as a triage problem: given limited frontline screening capacity, which children should be prioritised for full KPSP administration? Using an age-matched case–control design, an interpretable Random Forest model distinguished clinically ascertained developmental delay cases from community controls on the basis of questionnaire risk factors alone — child and family demographics, perinatal history, parenting style, stimulation practices, and screen time — with no developmental test items used as features (accuracy 0.852 ± 0.082, precision 0.890 ± 0.129, recall 0.750 ± 0.198, F1-score 0.791 ± 0.141 under repeated stratified five-fold cross-validation), outperforming logistic regression and decision tree baselines. Screen time was the dominant predictor, followed by child age, household smoking exposure, birth weight, child sex, and authoritative parenting.

Three qualifications bound the result, and they are part of the contribution rather than disclaimers. First, because cases were recruited through a therapy clinic and controls through a posyandu, recruitment-channel confounding is quantified and addressed directly: adding socioeconomic features raised unmatched-sample performance to accuracy 0.983, showing that part of the case–control contrast tracks recruitment channel, so those features are excluded from the primary model and the confound is bounded through a channel-only baseline, socioeconomic matching, and a channel-invariance check `[[TO BE COMPUTED: channel-only baseline, SES-matched metrics, within-channel importance rankings]]`. Second, a model that produces risk scores without calibration and net-benefit evaluation cannot support a deployment decision; calibration and decision-curve analyses relative to screen-all and KPSP-only strategies are therefore reported as part of the primary result `[[TO BE COMPUTED: calibration slope/intercept, Brier score, net benefit at candidate thresholds]]`. Third, the secondary analysis on KPSP-screened community children showed that the same questionnaire factors do not reproduce screening outcomes in an unselected population (recall of the at-risk class 0.15); questionnaire-based risk modelling does not replace developmental screening. Taken together, these results position the model as a pre-screening triage aid that prioritises children for full KPSP assessment and referral, and they delimit the boundary beyond which such a model should not be used — a boundary the existing machine learning literature on child health in Indonesia has not reported.

The parenting subscales require psychometric repair before parenting can enter any headline claim (α = 0.10, −0.18, 0.13 for authoritative, authoritarian, and permissive respectively; the ten-item stimulation scale was reliable, α = 0.789). Future work will therefore address a larger multi-site sample with the case and control arms recruited through comparable channels, anthropometric z-scores as additional features, a multi-item validated screen-exposure instrument with a dose-response check, prospective external validation at a second site, and a decision-threshold-optimised web-based prototype for frontline use.
