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eduKateSG · Why Mathematics? · Causal Reliability Analysis: Interventions, Confounding, Target Trials and Counterfactual Failure Risk
Start with the question, audit the worked example, or jump to the assumptions and practice. Every chapter stays open for uninterrupted reading.
Understand the question
Define the quantity and follow the mechanism.Route 2 · Chapters 10–18
Reproduce the example
Audit the numbers one step at a time.Route 3 · Chapters 19–27
Check assumptions
See where design and calibration matter.Route 4 · Chapters 28–36
Explore applications
Connect the method to a concrete investigation.Route 5 · Chapters 37–46
Study and verify
Practise, inspect failure cases and read further.
Full chapter index · Practice and checking · Mathematics Learning Hub
Why is mathematics important in causal reliability analysis? Predicting which machine will fail does not show what maintenance, design or load intervention will prevent failure. Causal mathematics separates association from intervention through potential outcomes, directed graphs, target trials and explicit assumptions.
This guide develops confounding, standardisation, time alignment, weighting and sensitivity with practical examples. Real interventions require engineering mechanism evidence, safety constraints and competent review.
Full chapter index
Chapters 1–9 · Understand the question
Chapters 10–18 · Reproduce the example
Chapters 19–27 · Check assumptions
Chapters 28–36 · Explore applications
Chapters 37–46 · Study and verify
CHAPTER 1 OF 46 · Understand the question
1. Prediction and intervention are different
A predictive model asks which units are likely to fail. A causal model asks what would happen if we changed maintenance, load or design. A warning signal can predict failure without being a safe intervention target.
Let Y(1) be failure status by a horizon under a specified intervention and Y(0) under comparison. Each unit reveals only one potential outcome. Causal inference uses design and assumptions to compare the unseen counterfactuals.
Choose average treatment effect, risk ratio, survival difference, restricted mean life difference or another target. Specify population, intervention versions, horizon and competing events. “Maintenance effect” is too vague.
The observed outcome equals the potential outcome under the intervention actually received when the intervention is well defined. Different overhaul procedures cannot be collapsed into one treatment without defending equivalence.
After conditioning on measured confounders, treated and untreated units should be comparable in potential outcomes. Randomisation can support exchangeability; observational maintenance data usually require strong assumptions.
Every relevant covariate pattern needs a positive chance of each compared intervention. If critical assets always receive preventive maintenance, data cannot identify their no-maintenance outcome without extrapolation.
One unit’s maintenance may change another’s risk through shared load, crew or spares. Standard no-interference assumptions then fail. Define clusters or system-level interventions.
High-risk assets are maintained more often because engineers see warning signs. A naïve comparison can make maintenance look harmful. Condition on pre-action risk indicators without adjusting for consequences measured afterward.
A DAG encodes assumed causal arrows among load, warning, maintenance and failure. It helps identify backdoor paths and data needed for adjustment. The graph is a reasoned assumption, not a discovery from correlations alone.
If condition C causes both maintenance A and failure Y, adjust for C to block A←C→Y. Standardisation, regression or weighting can estimate effects when the adjustment set and models are adequate.
Suppose 40% of assets are high risk. Failure under maintenance is 0.10 high-risk and 0.05 low-risk, giving 0.4×0.10+0.6×0.05=0.07. Without maintenance it is 0.4×0.25+0.6×0.10=0.16. Standardised risk difference is -0.09.
| Stratum | Population share | Maintained | Unmaintained |
|---|---|---|---|
| High risk | 0.40 | 0.10 | 0.25 |
| Low risk | 0.60 | 0.05 | 0.10 |
| Standardised total | 1.00 | 0.07 | 0.16 |
The same illustration gives risk ratio 0.07/0.16=0.4375. Relative and absolute effects answer different questions. The numbers are illustrative and require exchangeability, positivity and consistent interventions.
If both maintenance and failure cause an investigation report, conditioning only on reported cases opens a noncausal association. Do not adjust for every available variable; use the DAG and timing.
Maintenance may reduce vibration, which reduces failure. Adjusting for post-maintenance vibration blocks part of the total effect. Mediation questions require their own estimands and assumptions.
Classifying a unit as “maintained” using a future maintenance event gives it guaranteed survival until that event. Align eligibility, assignment and time zero. Treat maintenance as time-varying when appropriate.
Specify the hypothetical randomised trial: eligibility, strategies, assignment, time zero, follow-up, outcome, causal contrast and analysis. Then emulate these components with observational records and list deviations.
For a one-time action at commissioning, compare clearly defined strategies from a common time zero. Baseline confounders are measured before assignment.
Repeated inspection and maintenance depend on evolving condition that is also affected by prior maintenance. Ordinary regression adjustment can bias effects. Marginal structural models or the parametric g-formula may be needed.
Weight each observed treatment history by the inverse probability of receiving it given past covariates. This creates a pseudo-population with balanced measured histories under correct models. Extreme weights signal poor positivity.
| Assumption | Operational check |
|---|---|
| Consistency | Define intervention versions |
| Exchangeability | Measure pre-action confounders |
| Positivity | Inspect treatment overlap |
| Interference | Model shared load and resources |
Model outcome evolution under observed histories, then simulate outcomes under each intervention strategy. Flexible models reduce form error but do not remove unmeasured confounding.
An instrument changes treatment but affects outcome only through treatment and satisfies independence assumptions. Technician preference or scheduling rules rarely qualify automatically. State and test implications where possible.
A strict threshold rule can support local causal estimates near the cutoff if units cannot manipulate the running variable and other factors change smoothly. It answers a local effect.
Compare before-after changes in treated and comparison groups under parallel-trends assumptions. Design changes and anticipation can violate the assumption. Plot pre-trends.
Randomly assign maintenance intervals, software versions or design features when ethical and feasible. Randomisation addresses measured and unmeasured confounding on average, but noncompliance, censoring and interference remain.
Loss to follow-up can depend on risk and treatment. Use inverse probability of censoring weights or joint models under explicit assumptions. Administrative censoring still limits long-horizon effects.
Replacement, retirement or another failure can preclude the event. Define whether the causal estimand concerns cause-specific hazard, cumulative incidence or a composite outcome. Intervention may affect competing events too.
Compare survival curves, risks at horizons or restricted mean time. Hazard ratios are noncollapsible and can change with survivor composition, making them difficult causal summaries.
Random forests, boosting and Cox models can estimate nuisance functions or heterogeneous effects, but predictive accuracy alone does not identify causality. Cross-fitting can reduce overfitting while causal assumptions remain essential.
The maintenance-optimisation article compares policies under lifetime and cost models. Causal evidence helps estimate what policy changes would do.
The FRACAS data article emphasises exposure and action histories. Causal analysis also needs pre-action confounders and aligned timestamps.
Treatment benefit may vary by condition, age or environment. Estimate subgroup effects only with overlap and enough events. Flexible causal forests need honest validation and multiplicity caution.
An outcome or exposure that should not be causally affected can reveal residual bias. A null negative control does not prove all assumptions, but a nonnull result warns against causal confidence.
Quantify how strong an unmeasured confounder or selection effect must be to change the conclusion. Vary intervention definitions, lag periods, weights and outcome coding.
An effect estimated in one fleet may not transfer when design, crew or environment differs. Define the target population and reweight or model effect modifiers with uncertainty.
Reproduce standardised risks 0.07 and 0.16, difference -0.09 and ratio 0.4375. Check temporal order, treatment coding, time zero, weight formulas and positivity diagnostics.
Compare results across randomised evidence, natural experiments, mechanistic models and differently biased observational designs. Agreement strengthens confidence; disagreement should trigger investigation.
Draw a DAG with condition causing both maintenance and failure. Calculate the standardised example. Then show how conditioning on a post-action mediator changes the question.
Imagine comparing students who chose tutoring with those who did not. The groups differed before tutoring, so outcomes alone do not reveal the effect. The same logic applies to preventive maintenance.
CHAPTER 39 OF 46 · Study and verify
39. Common misconception: adjustment makes data causal
Adjustment works only for a sufficient set of accurately measured pre-action confounders with overlap and correct modelling. More variables can introduce collider bias.
CHAPTER 40 OF 46 · Study and verify
40. Common misconception: feature importance is intervention effect
Importance describes a predictor’s role in a fitted model. It does not estimate what happens when an engineer changes that feature.
The highest-risk machines can make a useful maintenance programme look ineffective because they are precisely the machines selected for treatment. This is confounding by indication.
No. Safety, cost and operations can prevent it. Target-trial emulation and natural experiments improve observational work while preserving honest limitations.
No. It estimates effects under assumptions and data. Safety decisions also require physical evidence, standards, hazard analysis and competent review.
Report causal question, population, DAG, intervention versions, comparator, eligibility, time zero, outcome, horizon, estimand, confounders, positivity, interference, censoring, competing risks, estimator, diagnostics, sensitivity, transportability and uncertainty.
Hund and Schroeder present a causal perspective on reliability assessment. Vanderschueren and colleagues study preventive-maintenance frequency with causal machine learning.
Mathematics matters because changing a system is not the same as predicting it. Causal reliability analysis aligns interventions, timelines and assumptions so maintenance and design decisions rest on more than association.
Extended practice laboratory
Work through the cases in design order. Define the target trial and draw the causal graph before estimating a propensity score or outcome model. Use the standardisation example to make the target population explicit, then compute absolute and relative effects from the same counterfactual risks. Inspect collider, mediator and immortal-time examples to see how apparently helpful adjustments can change the question or introduce bias. Only then examine overlap, weights and sensitivity. Preserve a table with intervention versions, eligibility, time zero, follow-up, outcome, estimand, adjustment set and diagnostics. Add at least one alternative graph and explain which conclusions depend on it. Triangulate with operational knowledge, negative controls and any randomised or quasi-experimental evidence. The exercise is complete when the causal claim remains narrower than the predictive claim: forecasting which assets fail and estimating what maintenance would change are connected but separate mathematical tasks.
Students can practise causal reasoning with ordinary choices—study plans, transport or equipment care—while avoiding claims that one observation proves an effect. Parents can ask what happened before the action, why people received different actions and what fair comparison is missing. Those questions develop statistical literacy without requiring advanced software. They also show why mathematics supports careful decisions: formulas organise a claim, but design knowledge determines whether the comparison deserves a causal interpretation. A final check should always name one plausible alternative explanation and one new observation or experiment that could distinguish it.
Practice case 1: Standardised maintenance
Setup: Use high-risk share 0.4 and maintained risks 0.10,0.05.
Task: Calculate weighted risk.
Checking target: Obtain 0.07.
Standardisation combines stratum-specific counterfactual risks using a common target population. With 40% high-risk and 60% low-risk units, maintained risks 0.10 and 0.05 give 0.4(0.10)+0.6(0.05)=0.07. Write the target shares separately from the outcome risks so they are not accidentally replaced by treatment-group composition. This calculation estimates the maintained risk only if measured covariates are sufficient for exchangeability, the intervention is consistently defined and every relevant stratum has support. Reproduce the weighted terms before summing and test that weights total one. In data, obtain risks from a suitable outcome model or design, not from invented cells. Report uncertainty and consider clustering by site or asset. Standardisation makes the estimand transparent; it does not make unmeasured confounding disappear.
Practice case 2: Standardised comparison
Setup: Use unmaintained risks 0.25,0.10.
Task: Calculate weighted risk.
Checking target: Obtain 0.16.
Using the same target shares, unmaintained risks 0.25 for high-risk units and 0.10 for low-risk units give 0.4(0.25)+0.6(0.10)=0.16. Keeping the population weights identical is essential because the comparison asks what would happen to the same population under two strategies. If each observed action group were averaged with its own composition, baseline condition could masquerade as an effect. Check every cell's sample size and positivity before trusting model-based estimates. Vary the target population to see how transport changes the marginal risk, but label the new estimand. A real maintenance strategy also needs timing, eligible assets and permitted intervention versions. The arithmetic is only the last step of a design that must align assignment, follow-up and outcome measurement.
Practice case 3: Risk difference
Setup: Subtract 0.16 from 0.07.
Task: Calculate effect.
Checking target: Obtain -0.09.
The standardised risk difference is 0.07-0.16=-0.09, or nine fewer failures per 100 units by the horizon under the maintained strategy in this illustration. Preserve the sign by writing maintained minus unmaintained before substitution. Risk difference is an absolute effect and can support resource planning, but only for the stated population and horizon. Add confidence intervals and sensitivity analyses rather than presenting -0.09 as exact. If failure is rare or consequences vary widely, counts alone may not capture utility; combine the effect with cost and severity in a separate decision model. This example is not evidence that any specific programme achieves the reduction. Its purpose is to show how a clear estimand turns stratum-specific risks into an interpretable population contrast.
Practice case 4: Risk ratio
Setup: Divide 0.07 by 0.16.
Task: Calculate effect.
Checking target: Obtain 0.4375.
The risk ratio is 0.07/0.16=0.4375. Under the illustration, maintained risk is about 44% of unmaintained risk, corresponding to a relative reduction of about 56%. State which risk is numerator and denominator, and always report the underlying absolute risks because a dramatic ratio can accompany a tiny absolute change. Ratios also become unstable when the denominator is near zero. Compare the ratio with the risk difference and, if relevant, a survival contrast across time. Do not call 0.4375 a hazard ratio; hazards and cumulative risks are different quantities. Verify the division and rounding independently, then explain how the measure would change if the target population or horizon changed. Effect measures answer complementary questions rather than competing for a single 'best' summary.
Practice case 5: DAG
Setup: Draw condition causing action and failure.
Task: Identify the backdoor path.
Checking target: Adjust for pre-action condition.
Draw a directed acyclic graph in which pre-action condition affects both maintenance assignment and later failure. The path maintenance <- condition -> failure is a backdoor path that can confound an observed association. Adjustment for a well-measured pre-action condition can block this path under the graph, while adjusting for descendants may create other problems. Mark time order on every node and include shared load, site and prior repair when scientifically plausible. The graph is a statement of assumptions, not something proven by the dataset. Compare alternative credible graphs and identify the adjustment set each implies. Check whether variables are measured before treatment and with sufficient quality. A predictive feature list is not an adjustment strategy: the goal is to block biasing paths without conditioning on mediators or colliders.
Practice case 6: Collider
Setup: Make reporting caused by action and failure.
Task: Condition on reporting.
Checking target: Explain the opened path.
Suppose reporting is caused by both maintenance activity and failure severity. Conditioning the analysis on reported cases makes reporting a collider on maintenance -> reporting <- severity. Selection can then open an association between maintenance and severity even when none existed. Demonstrate with a simple table or simulation: generate independent causes, select only rows where reporting occurs, and inspect the induced correlation. The remedy is not automatically to adjust for more variables; it is to redesign sampling or model the selection process using defensible information. Identify all filters applied before analysis, including complete-case rules, inspection attendance and ticket closure. Collider bias often enters through data assembly rather than an explicit regression term. A transparent cohort flow diagram helps reviewers see where selection could have changed the causal question.
Practice case 7: Mediator
Setup: Put vibration after maintenance.
Task: Choose total or direct effect.
Checking target: Do not adjust automatically.
If maintenance changes vibration and vibration then affects failure, vibration is a mediator. Adjusting for it while estimating the total maintenance effect can remove part of the pathway the total effect is meant to include. If the question is a controlled or natural direct effect, additional assumptions and careful definitions are required. Draw the temporal path and state the estimand before selecting variables. Distinguish pre-action vibration, which may confound assignment, from post-action vibration, which may mediate benefit; identical column names at different times can play different roles. Fit total-effect and mediation analyses only when data and assumptions support them. The practice exposes why 'include every predictive variable' is unsafe for causal work. Variable timing and the target contrast govern adjustment.
Practice case 8: Time zero
Setup: Align eligibility, assignment and follow-up.
Task: Remove immortal time.
Checking target: No unit earns treatment status from the future.
Eligibility, strategy assignment and follow-up must begin at the same time. If an asset is classified as maintained only after surviving long enough to receive maintenance, the pre-maintenance survival period becomes immortal time and biases the maintained group. Emulate a target trial by defining time zero, eligibility, strategies, grace periods and assignment rules prospectively. Use cloning, censoring and weighting or another appropriate method when strategies evolve over time. Draw timelines for several assets and verify that no outcome time is credited to a future treatment status. A naive 'ever maintained' label is a warning sign. The correction should be chosen from the causal design, not by shifting timestamps until results look reasonable. Report deviations from assigned strategy and how they enter the estimand.
Practice case 9: Positivity
Setup: Find covariate groups with one action only.
Task: Inspect propensity scores.
Checking target: Do not extrapolate silently.
Positivity requires a nonzero chance of each strategy within covariate patterns needed for the target contrast. Estimate and plot propensity scores by action, then inspect regions with little overlap. A site that always replaces a certain component provides almost no direct evidence about not replacing it there. Flexible models cannot manufacture that counterfactual. Consider narrowing the target population, coarsening the intervention or collecting new data rather than extrapolating silently. If weights are used, examine their tails and effective sample size. Trimming changes the target estimand and should be declared. Structural absence of an action differs from random small-sample sparsity, but both reduce support. Positivity assessment is therefore a design check before effect estimation, not merely a cosmetic diagnostic after fitting.
Practice case 10: Weighting
Setup: Calculate inverse treatment weights.
Task: Check balance and tails.
Checking target: Trim only with a declared estimand change.
For inverse treatment weighting, a maintained unit may receive 1/e(X) and an unmaintained unit 1/[1-e(X)], with stabilised variants often preferred. Calculate weights from a propensity model using pre-action covariates, then check weighted balance rather than relying on model fit. Plot distributions, tail quantiles and effective sample size. Large weights reveal weak overlap and can dominate the estimate. Truncation may reduce variance but introduces a different bias-variance trade-off; report several thresholds and the implied population. Use cluster-robust uncertainty when assignments or outcomes share sites. A good propensity model is one that supports balance for the causal design, not necessarily the one with the highest predictive accuracy. Preserve the model specification and balance diagnostics so another analyst can reproduce the pseudo-population.
Practice case 11: Sensitivity
Setup: Vary an unmeasured-confounding scenario.
Task: Recalculate the effect.
Checking target: Report when conclusions change.
Sensitivity analysis asks how strong an unmeasured factor would need to be to change the conclusion. Specify a plausible confounder prevalence and its association with action and failure, then recalculate the effect across a grid. Alternatively use a recognised bias formula or negative-control analysis suited to the design. Do not report a single favourable scenario. Show where sign, magnitude or practical decision changes, and connect parameter ranges to engineering knowledge. Sensitivity analysis does not prove absence of bias; it maps dependence on assumptions that the observed data cannot test directly. Include measurement error, intervention misclassification and informative censoring when those threats matter more than hidden confounding. A conclusion is more credible when it says which departures it can tolerate and which would overturn it.
Practice case 12: Conclusion
Setup: State intervention, comparator and estimand.
Task: Report assumptions and triangulation.
Checking target: Do not equate prediction with cause.
The conclusion begins with population, intervention, comparator, time zero, horizon and estimand. It states the identification assumptions—consistency, exchangeability, positivity and interference conditions—and shows how design and analysis addressed them. Report absolute risks with effect contrasts and uncertainty, then summarise overlap, balance, negative controls and sensitivity results. Triangulate with randomised, quasi-experimental or mechanistic evidence when available. Keep predictive evidence separate: a variable can forecast failure without being a useful intervention target, and feature importance is not a causal effect. Avoid guaranteeing safety or savings from one observational estimate. Preserve cohort construction code, data dates, intervention versions and diagnostics. The strongest claim is the narrowest one the design can support, paired with a clear plan for further testing and monitoring.