RESEARCH DOSSIER
Insurance Advice Experiment Design and Consumer Outcome Measurement
Abstract. Insurance advice changes the relationship between a consumer's underlying exposure to loss and the contractual protection eventually obtained. Its causal evaluation therefore requires an intervention defined at the point of recommendation, a defensible counterfactual, a pre-specified assessment of contract suitability, and follow-up that distinguishes enrollment from sustained protection and realized financial outcomes. This monograph develops an integrated methodological account of adviser prompts, disclosure order, recommendation tools, suitability checks, and independent quality assurance. It synthesizes field experiments in retail life and health insurance, international supervisory evidence, and established methods of randomized and quasi-experimental inference. It examines allocation concealment, adviser-level contamination, heterogeneous treatment effects, measurement invariance, selective enrollment, claims selection, attrition, and ethical safeguards. A worked cluster trial, an outcome dictionary, and a reproducible analysis specification illustrate the operational consequences. The central conclusion is that recommendation quality, consumer understanding, in-force coverage, and household welfare must be measured as distinct outcomes within a common causal design. A gain in conversion or predicted cost alone establishes neither effective protection nor consumer welfare. The work is a critical methodological synthesis with hypothetical examples; it reports no newly conducted trial, regulatory permission, or empirical effect estimated from original participant data.
Keywords: Insurance advice; insurance distribution; consumer outcomes; field experiments; cluster randomization; causal inference; suitability; comprehension; claims; consumer protection; longitudinal measurement; market conduct.
Introduction
Insurance distribution is an allocation mechanism for contingent financial protection. An adviser may help a customer recognize an exposure, interpret contract language, compare suppliers, reconcile cover with a limited budget, or avoid a product incompatible with the customer's circumstances. The same transaction may also expose the customer to a conflict of interest, an unnecessary replacement, an incorrectly specified insured interest, or a deductible beyond available liquidity. Experimental evaluation must consequently begin with the risk transfer purchased and the alternatives displaced, rather than with the amount of business written.
Consider two households buying otherwise comparable property cover. One obtains a lower premium by accepting a deductible its savings can support; the other appears to obtain the same saving by accepting a deductible that would prevent repair after a loss. A sales dashboard records equal premium reductions. A protection analysis identifies different consequences. The relevant counterfactual includes the feasible alternative policies, the states in which payments become due, the resources available at those times, and the possibility that declining to buy a particular product is appropriate. A scientific study of advice must preserve this economic structure at the point of measurement.
The independent research object is the causal evaluation of an intervention in the advice process and its consequences for consumers. An audit of static recommendation quality establishes whether advice was consistent with a stated profile. Mystery shopping observes how a specified encounter is handled. A choice-architecture experiment may alter a menu without involving an adviser. Each can contribute evidence to a causal study, but the present work concerns comparisons between defined interventions in advice and the subsequent trajectories of consumers exposed to them.
The evidence base is a purposive critical synthesis, not a systematic review with a registered search protocol or pooled effect size. Sources were identified through targeted searches for insurance advice field experiments, health-plan choice, supervisory monitoring, research ethics, experimental allocation, interference, instrumental variables, and sample selection. Institutional publications and original study abstracts are distinguished from full text. The research designs, outcome specifications, equations, and worked numbers below are methodological applications and authorial illustrations. Observational supervisory evidence is used to define problems and testable questions, not to claim intervention effects. Findings from different insurance products and countries are kept separate.
Three questions organize the analysis. First, how can investigators construct credible comparisons between legally and ethically acceptable advice procedures? Second, which measures distinguish immediate recommendation quality from protection after enrollment? Third, what inference remains defensible when assignment, intervention receipt, policy selection, claims, and observation of outcomes occur at different levels and times?
Advice Interventions and Experimental Estimands
The intervention as an observable institutional action
An intervention is a versioned change in the advice process applied to a defined population within a defined distribution channel. It may consist of a prompt requesting an explanation of major exclusions, a structured needs-assessment form, a comparative premium and deductible display, a recommendation aid, a requirement for independent second review, or a revised sequence of mandatory disclosures. Every treatment specification should include the software or script version, actor responsible, timing, exceptions, training materials, available product universe, and authority to override. Specifying the treatment as better advice is scientifically insufficient because multiple operational changes could satisfy that description.
A useful experimental contrast is an approved standard process versus that process plus a targeted enhancement. A prompt about emergency savings may change the deductible selected without changing the products offered. A structured comparison may make a broker's restricted panel more transparent without expanding it. A quality-control intervention may identify mismatches and trigger correction before binding. These are different treatments, with different mechanisms and costs. An intervention that simultaneously changes products, commission rates, staff allocation, and communication cannot identify the independent contribution of any one component without additional variation.
The same distinction applies to interventions aimed at advisers and those aimed at customers. An adviser prompt changes what is elicited and recorded. A consumer comparison aid changes information available at the decision stage. A supervisor's feedback changes the institution's monitoring and incentives. If a customer is exposed to all three, a factorial design may identify component effects when the components can be ethically and operationally separated. Otherwise a package comparison answers a pragmatic question about the combined procedure.
Evidence from actual insurance experiments
Anagol, Cole, and Sarkar (2017), in their study of commission-motivated life insurance agents in India, report advice favoring high-commission products that were unsuitable under the study's profiles. Their abstract also describes a product-specific disclosure change followed by recommendations of alternative high-commission products that were outside that disclosure requirement. The evidentiary contribution is direct observation of advice behavior and substitution under a limited regulatory intervention. The published abstract supports these qualitative results; it does not support a universal incidence estimate for mis-selling or a claim about realized household welfare after years of coverage.
Kling et al. (2012) investigated comparison friction in Medicare drug plans using a personalized information letter. The reported switching rates were 28 percent in the intervention arm and 17 percent in the comparison arm; predicted annual consumer cost fell by about $100 among letter recipients. These are study-specific results in U.S. Medicare Part D, not observed universal savings from insurance intermediaries. An information letter is an adjacent intervention rather than a full regulated advice encounter. Nevertheless, it identifies a practical mechanism: reducing the effort required to use available information can change actual insurance choices.
Bundorf, Polyakova, and Tai-Seale (2019), in the institutional summary of their algorithmic advice experiment, describe changes in plan choice and costs together with systematic selection into participation. The working-paper summary indicates that a decision-support tool may alter both behavior and engagement. Its lesson for pragmatic advice evaluation is that an offer to use a tool and exposure to the tool are different statistical events. A favorable response among willing users can coexist with limited population benefit when those most likely to benefit are hard to reach. The cited version is a working-paper summary, so precise numerical estimates and subsequent publication changes are outside the claims made here.
These studies concern different institutions, treatments, populations, and endpoints. No weighted average of their results is meaningful without a harmonized estimand and compatible data. Their shared analytical significance is the need to identify which action changed, which population received it, and which consequence was actually measured.
Assignment, treatment receipt, and policy selection
Let i index a customer or household and Z_i denote randomized assignment, with Z_i = 1 for the enhanced process and Z_i = 0 for the standard process. Let D_i represent actual receipt of a specified component, and Y_i(t) an outcome measured by time t. When assignment is randomized, the intention-to-treat effect at horizon t is
ATE_ITT(t) = E[Y_i(t) | Z_i = 1] - E[Y_i(t) | Z_i = 0].
Under consistency, random assignment, and an appropriate treatment of interference, this identifies the average effect of offering or assigning the enhanced process in the trial population. The estimand is policy-relevant because a distribution organization controls assignment more directly than it controls customer uptake. All eligible participants remain in their allocated group, including those who decline the aid, receive an override, or decide against a purchase.
Receiving a recommendation, accepting it, obtaining a policy, and maintaining the policy are later actions. Restricting the main analysis to customers who buy a product conditions on an outcome that may itself respond to the intervention. If Z affects purchase and underlying needs influence both purchase and losses, customers who purchase in the two arms can have different risk profiles even under ideal randomization. The comparison among purchasers no longer inherits the original experimental balance.
An encouragement design offers a voluntary component without requiring uptake. The effect of the offer is directly identifiable under randomization. A complier effect requires further assumptions, including a relevant first stage, exclusion of alternative effects of assignment, monotonicity, and an interference specification. A reminder that improves general financial attention may influence the outcome even without software use; exclusion is then implausible. The study should report the offer effect rather than force a causal estimate of tool receipt.
Time, population, and decision criteria
A complete estimand specifies the eligible population, treatment version, comparison version, outcome definition, horizon, summary measure, and treatment of events that intervene between recommendation and assessment. If the goal is appropriate protection six months after a renewal, the denominator includes all renewal-eligible consumers and a pre-defined treatment of customers whose exposure ended. If a customer moves away from an insured property, nonrenewal need not represent failure. Conversely, where a customer remains exposed, a cancellation or unresolved lapse may be a meaningful adverse outcome.
A primary outcome can be the fraction of eligible households with required or otherwise appropriate protection in force at day 180, assessed under a pre-registered rubric. Secondary outcomes may include comprehension, material advice errors, time to bind, costs, coverage gaps, and unresolved claim delays. Regulatory violations and serious foreseeable consumer harms should be tracked as safety outcomes regardless of statistical significance. Increasing one primary metric at the cost of a substantial safety deterioration is not an acceptable implementation decision.
A causal estimate quantifies an intervention under its stated design. Adoption requires a separate institutional judgment concerning costs, legality, equity, scalability, and material risks. A statistically precise increase in recommendation acceptance can be operationally undesirable if acceptance is attributable to undue pressure. The endpoint that guides the decision must embody the research purpose.
Experimental Ethics and Consumer Protection
Legal compliance as a design constraint
Advice experimentation takes place within a market in which real consumers may incur lasting consequences. The first design step is to identify a set of permissible procedures. Both the standard and enhanced procedures must satisfy the laws, product obligations, licensing requirements, and protections applicable to their actual use. A trial cannot create a legal exemption by labeling an omission a control condition.
In the European Union, Article 20 of the IDD establishes a demands-and-needs requirement and additional requirements where advice is supplied. For insurance-based investment products, Article 30 of the IDD adds specific suitability or appropriateness provisions subject to the directive's conditions and exceptions. These instruments illustrate why experiment designers must distinguish sales with advice from sales without advice and verify national implementing rules. The general demands-and-needs assessment and the investment-product suitability assessment are distinct legal constructs.
An intervention may test two compliant ways of communicating a required exclusion. It should not suppress legally required information from one arm. A simulation can test comprehension of an incomplete hypothetical explanation without authorizing a real transaction; the ethics review should consider deception, debriefing, and any opportunity cost imposed on participants. The trial designer should document who has determined that the baseline is compliant and who can halt the study if that determination becomes invalid.
If the organization has clear evidence that its existing sales process causes avoidable harm, preserving it solely for comparison may be unethical. An immediate correction, followed by a comparison between permissible enhancements, is preferable. Where rollout is necessarily gradual, a randomized schedule may be considered only after examining whether delayed access introduces unacceptable harm and whether ordinary operational constraints create genuine equipoise. A stepped rollout is not a license to prolong a known harmful practice.
Consent, risk, and justice
The 1979 Belmont Report identifies respect for persons, beneficence, and justice as ethical foundations and relates them to consent, risk-benefit evaluation, and fair participant selection. Its use here is an ethical reference, not an assertion that every private insurance quality-improvement study falls under U.S. federal human-subject regulations. Local law, institutional research policies, data protection, and the intended dissemination of results determine the required review.
A consent process should explain which information is used, whether advice encounters may be recorded, how long administrative follow-up lasts, what withdrawal means, and whether service remains available to nonparticipants. Consent to insurance coverage does not automatically constitute consent to research or unrelated use of customer data. A transfer of data between broker, insurer, and independent research organization requires its own lawful authority and governance.
A consumer who declines research participation should still receive the applicable advice and service standard. Recruitment should avoid making a needed policy contingent on research participation. Accessible formats and reasonable adjustments should be available across arms. Excluding everyone with low literacy can reduce operational risk at the cost of producing evidence for a population unlike the one the intervention is intended to help. The appropriate response is to design safe support and sufficient representation, not to expose participants to unsuitable cover.
Safety monitoring and independent correction
Before recruitment, specify adverse events: an uncovered mandatory or material exposure after advice, a customer induced to terminate essential cover without a feasible replacement, a documented materially misleading explanation, an inappropriate investment or surrender recommendation, a privacy incident, or credible evidence of undue pressure. Define severity, immediate response, responsibilities, and reporting deadlines. A qualified reviewer independent of the sales target should be empowered to veto a proposed contract or arrange correction.
An alert should lead to protection of the affected customer rather than waiting until statistical analysis. Remediation has two roles: it is a safety action and an observable event within the assigned process. When an independent review stops a proposed unsuitable purchase, record the initial recommendation, the reason, the correction, and the eventual position. Excluding corrected cases from the analysis would disguise a safety function that may constitute much of the benefit of the treatment.
Define stopping criteria for severe individual events and arm-level patterns before trial initiation. A single severe event may require immediate escalation regardless of statistical testing. Thresholds for less severe events should incorporate baseline frequency and uncertainty; they must not encourage repeated unplanned significance searches. Analysts who monitor outcomes for safety should distinguish operational decisions from confirmatory efficacy inference. Report any changes to the protocol and the circumstances that caused them.
Conflicts of interest and research governance
The sponsor may prefer higher conversion, the adviser may prefer higher remuneration, and the consumer may prefer protection with acceptable cost. These objectives coincide in some transactions and conflict in others. A study financed by a distributor should protect analysis independence through a signed protocol, auditable assignment logs, documented outcome criteria, and permission to report unfavorable results. Adviser pay should not be tied to the primary consumer outcome in a way that incentivizes manipulating the measurement.
A successful intervention can induce substitution toward another product, commission category, or channel. For example, a prompt targeting one product's exclusions may lead advisers to favor a product outside the prompt's coverage even when its exclusions are similar. Track recommended alternatives, product identifiers, fees, and commissions where lawful. The unit of ethical accountability remains the real customer journey, including recommendations that did not lead to a contract.
Randomization Units and Cluster Spillovers
Choosing the allocation unit
Individual allocation is attractive when a comparison display can be shown independently to each customer and when the adviser behaves consistently regardless of earlier assignments. In advice settings, knowledge is often durable. An adviser trained to explain a hidden exclusion may apply that understanding to later control clients. Randomizing separate clients served by the same adviser can therefore dilute the contrast, alter the meaning of the control, or produce effects that depend on the order of appointments.
Cluster randomization assigns advisers, teams, agencies, branches, or geographic offices to a process version. Its rationale is protection against contamination and alignment with the intervention's delivery. A branch receives an enhanced workflow that all eligible advisers use; the comparison branch retains its approved workflow. Customers are analyzed in accordance with the assigned cluster, and the variance calculation recognizes dependence among customers in that cluster.
The correct cluster level depends on actual communication, staff mobility, common management, software access, and customer referrals. A franchise network with centralized daily coaching may transmit treatment across nominally distinct branches. A broker who works at multiple locations may carry training between them. A customer may receive advice from more than one employee. The study must map these links before allocation rather than treat organizational labels as evidence of independence.
The cluster CONSORT extension (Campbell et al., 2012) supplies a reporting precedent for distinguishing the levels of allocation and analysis. Adapt it to insurance research: state the number of clusters, eligible advisers and customers, recruitment timing, assigned clusters, customer flow, outcome observations, and clustering assumptions. Clinical reporting guidance provides a useful methodology; it is not an insurance-specific regulatory requirement.
Assignment integrity and contamination
Prepare a baseline list of clusters and the eligible customer frame before randomization where possible. Stratify on characteristics that predict outcomes or implementation, such as channel, pre-intervention scale, product line, or historical coverage gaps. Excessive stratification with few clusters can create infeasible assignment blocks, so use a simple pre-specified allocation scheme. Store the random seed or reproducible assignment procedure and conceal the allocation from anyone who can manipulate recruitment.
If consumers are recruited after advisers learn allocation, advisers might preferentially invite customers who are easier to serve. Enroll objectively defined appointment cohorts or retain administrative records of the complete eligible frame; compare recruitment and exclusions across arms. Balance tests should be descriptive, not post-randomization criteria for discarding unfavorable allocations. Analyze using the actual randomization scheme, including pairs or strata if they were used.
Interference occurs when an outcome depends on other participants' assignments. Hudgens and Halloran (2008) develop causal inference with interference beyond the no-interference setting. In insurance, training can spill between advisers, customers can share recommendations, and a change in demand can affect queue length or product capacity. Under partial interference, clusters may be assumed to interact internally but not with one another. This assumption requires justification by operational evidence.
A two-stage saturation experiment can assign clusters to different proportions of treated members and then randomize within those clusters. It may estimate direct and indirect effects under a stated exposure mapping, provided there are enough clusters and both assignment stages are implemented as designed. It is unnecessary where a straightforward cluster-level policy effect answers the research question. In that case, internal spillovers are part of the bundled intervention's effect. Cross-cluster movement should still be measured and reported.
Power and sample size
For a simple binary primary endpoint with control probability p0, treatment probability p1, equal allocation, two-sided type I error alpha, and target power 1-beta, a normal approximation for independent observations is
n_arm = [z_(1-alpha/2) sqrt(2 pbar (1-pbar)) + z_(1-beta) sqrt(p0(1-p0)+p1(1-p1))]^2 / (p1-p0)^2,
where pbar = (p0+p1)/2. For equally sized independent clusters with an exchangeable intracluster correlation rho and m evaluated customers per cluster, the approximate design effect is
DE = 1 + (m-1)rho.
These formulas are planning approximations, not guarantees; they assume adequate cluster counts, a specified effect scale, and compatible variance structure. They should be followed by design-specific simulation or appropriate finite-sample calculations, especially for unequal cluster sizes, rare outcomes, and a small number of allocation units.
For illustration only, consider a baseline of 0.60 for an independently assessed suitable in-force policy and a target increase to 0.68. With alpha = 0.05 and 80 percent power, z values of approximately 1.96 and 0.8416 yield about 564 independent observations per arm. At m = 40 evaluated customers and rho = 0.03, DE = 2.17. The approximate requirement becomes 1,224 evaluated individuals per arm, or 31 clusters of 40 per arm after rounding. If 10 percent of customers are expected to lack an evaluable endpoint, recruiting 45 per retained cluster yields roughly 40.5 evaluated customers; possible whole-cluster dropout requires separate inflation. These hypothetical calculations should be recalibrated using actual baseline estimates and a small-sample correction. They are not evidence of the effectiveness or cost of any advice intervention.
Increasing customers within an already large cluster yields less additional information when the intracluster correlation is positive. A trial with 2,000 customers in four offices remains a study with only four randomized offices. A convincing confidence interval cannot be recovered by treating all customers as independent.
Alternative designs
A parallel cluster trial is suitable when training has persistent effects and a clean comparison can be maintained. A crossover design is appropriate only when the treatment can be removed and carryover is negligible or explicitly modeled; durable learning makes crossover particularly problematic for adviser education. A stepped-wedge design allocates implementation timing and may permit every site to eventually receive a permissible enhancement. It requires time effects, attention to anticipation, and careful separation of intervention effects from market trends.
Factorial allocation can evaluate two components, such as an adviser prompt and a personalized client summary, when each is permissible alone and in combination. The main effect of a component averages across the other component's assignment, while the interaction tests whether their joint effect differs from the sum of their separate effects on the selected scale. For a small number of sites a simpler two-arm evaluation may be more credible than an underpowered multi-arm design.
Suitability, Comprehension and Recommendation Fidelity
Construct validity and the benchmark
Suitability is a relationship between customer circumstances and contract characteristics. A rigorous assessment must start with an explicit information set available before the recommendation: exposure, property or liability characteristics, household resources, existing cover, constraints, legal requirements, relevant preferences, and feasible product alternatives. The benchmark should describe the acceptable range of recommendations rather than imposing a single contract when several products satisfy the consumer's objectives.
Three layers require separation. First, eligibility and hard constraints establish whether the consumer and exposure can be covered under policy terms and law. Second, coverage alignment assesses whether benefits, limits, exclusions, and deductibles address material needs. Third, affordability and preference alignment evaluate whether the proposed combination is sustainable and fits informed trade-offs. An otherwise suitable product may become unsuitable for a particular consumer because its premium or out-of-pocket exposure exceeds a credible budget.
A blinded panel can independently assess the record using a pre-specified rubric. Reviewers should have access to the same factual profile, product wording, and comparison set. They should be masked to assignment where possible. A material discrepancy between reviewers triggers independent adjudication. Store the original classifications and the adjudicated result. Report reliability, including agreement for the critical unsuitable category and uncertainty in disputed cases, rather than reporting an overall agreement rate that is dominated by easy cases.
A consumer's preferences and a reviewer's assumptions may diverge. For example, someone may rationally pay more for a network of clinicians that reflects an established treatment relationship. A comparison based solely on expected annual spending would misclassify such a choice. The benchmark should permit a documented trade-off if it is feasible, understood, and permitted. An objective dominance criterion is appropriate only if all material benefits and constraints are genuinely comparable.
Recommendation fidelity and process evidence
Recommendation fidelity concerns whether the stated procedure was performed and how closely it matched the treatment specification. Measure prompt presentation, response completion, adviser acknowledgment, explanation of the recommendation, product version, override, independent review, and time of delivery. These records establish what treatment exposure meant; they do not by themselves prove that the recommendation was reasonable.
When a prompt is omitted because a consumer urgently needs service, the deviation may be justified. A useful fidelity classification distinguishes technical failure, legitimate exception, adviser refusal, consumer refusal, and accidental crossover. Record the event without deleting the original assignment. Treat protocol compliance as a secondary outcome. An analysis adjusting for compliance after randomization may remove a mechanism through which the intervention works.
Unstructured notes can be useful for understanding why an adviser made a decision, but extraction rules must be frozen or their changes documented. If transcripts are automatically classified, validate the classifier against human-coded examples and check performance across languages, channels, and treatment arms. A prompt generating longer or more standardized text can make automatic detection easier even if substantive quality remains unchanged. The measurement system must test for differential classification error.
Objective comprehension and calibrated confidence
Comprehension testing should use questions that correspond to consequential contract decisions. Ask a customer to explain whether a defined event is covered, how a deductible or excess affects payment, which action is necessary to maintain coverage, and what happens when a claim is made. Use scenarios rather than mere recognition of phrases. Assessing knowledge of policy limits does not require a customer to memorize every exception; the study should focus on material terms and the ability to obtain accurate information when needed.
Immediate recall is fragile. Measure shortly after the encounter and again at a decision-relevant point, such as renewal or receipt of a policy document. A first comprehension test may itself educate the customer and affect later behavior. Give equivalent assessments in both arms, define any corrective feedback in advance, and consider a design that randomizes assessment timing if measurement effects are important and ethically permissible.
The FCA consumer understanding review (2026) documents the role of testing with real customers, feedback from multiple channels, accessible communication, and continued monitoring. This supports a measurement program that checks whether a communication change actually assists comprehension. The supervisory examples are not independent randomized evidence of efficacy and do not create additional legal requirements.
Confidence should be measured alongside correctness because the most consequential error may arise when a customer feels certain about an incorrect interpretation. A customer who knows that they do not understand an exclusion may seek help, while one who falsely believes that coverage applies may act on the error. Report the proportion of materially incorrect, high-confidence answers and the distribution of correct answers; avoid interpreting greater confidence alone as improvement.
Measurement invariance and accessibility
A questionnaire administered to diverse populations must represent the same construct across arms, languages, and modes. Plain-language versions, oral administration, and accessible interfaces should be available according to need. Compare item nonresponse, completion times, and error patterns. Where translation is necessary, check that the translated wording does not add or remove contractual meaning. A high reading-level test may estimate literacy more strongly than understanding of insurance protection.
A pretest can establish baseline knowledge, but it should be administered identically across arms. If a pretest highlights the very hazards the adviser intervention intends to address, it changes the experimental setting. The assessment plan should therefore document whether the target policy is the intervention alone or the intervention following a common baseline questionnaire.
From process audits to causal evidence
EIOPA's coordinated mystery shopping exercise (2025) studied insurance-based investment product interactions in eight EU member states during 2024. Its official results release describes standardized shopper questionnaires and a reported 84 percent of offered products matching at least one of the identified profile needs or objectives. That threshold does not establish that all material needs were met. The reported limited relationship between sales-process thoroughness and alignment gives an important reason to test targeted procedure changes rather than equate longer consultations with better protection.
A standardized fictional profile permits controlled comparison of recommendation quality across advisers. It cannot establish subsequent policy persistence, claims handling, or household welfare because a shopper encounter does not represent a real household followed through loss and renewal. A field experiment may incorporate blinded standardized encounters as an intermediate quality assay, while collecting longitudinal outcomes for consenting eligible consumers separately. The study should identify which data arise from each sample and never merge those units as if they were equivalent.
Coverage, Claims and Longitudinal Outcome Measures
Define the exposure before measuring the outcome
The consumer outcome begins before enrollment. Create a baseline unit of observation, such as eligible household, individual consumer, insured vehicle, business, or property. For each unit identify exposure, policy options, date of decision, existing coverage, and anticipated change in risk. For multiple policies per household, establish a hierarchy and aggregation rule; one household with three contracts should not automatically count as three protected households.
The timeline may include the first recommendation, formal quote, acceptance, underwriting, effective date, cancellation window, premium payments, endorsement, renewal, loss event, claim notification, settlement, and complaint or redress. At each time distinguish the consumer's risk exposure and the policy's actual state. A signed application may not bind insurance; a policy issued today may commence next week; an endorsement may remove a previously included exposure. Record effective and transaction times separately.
A continuing exposure that lacks appropriate in-force cover is a possible coverage gap. A household that no longer owns the insured asset may have no continuing exposure. A severe weather exclusion may leave a customer underinsured even when premium payments are current. The endpoint must incorporate material exclusions, limits, waiting periods, and ability to pay the retained loss. It must also distinguish an informed, lawful decision to retain risk from an unintended protection failure.
An outcome dictionary
The following proposed measures are examples for protocol selection. They are not a validated universal score.
| Measure | Numerator or recorded value | Denominator or unit | Principal interpretation limit |
|---|---|---|---|
| Materially unsuitable recommendation | Independent adjudication of one or more critical mismatches | All eligible advice encounters; disclose missing records | Quality at recommendation, not contract purchase |
| Comprehension | Correct consequential scenario responses | Eligible respondents and trial frame with missingness reported | Test performance, not actual loss experience |
| Enrollment | Consumers with effective new or renewed cover | Eligible assigned consumers | May include unsuitable cover |
| Appropriate cover at day 180 | Consumers satisfying pre-specified protection rubric | All assigned consumers with applicable exposure definition | Requires adjudicated coverage and handling of exposure exit |
| Protection gap duration | Days of material continuing exposure without specified cover | Eligible exposure-days | Depends on accuracy of exposure history |
| Out-of-pocket burden | Premiums and retained covered/uncovered losses, with settlement timing defined | Eligible households over fixed horizon | A realized cost is not expected utility |
| Claim notification rate | New valid claim notifications | At-risk exposure time | Frequency and reporting propensity both matter |
| Claim denial fraction | Denied closed claims | Eligible closed claims, with open cases separately | Selected claimants and case mix |
| Time to settlement | Time from specified claim event to payment or closure | Notified eligible claims, censoring explicit | Informative selection and competing closure |
| Complaint incidence | New complaints in a defined period | All eligible assigned consumers | Reporting accessibility and awareness influence counts |
| Remediation | Documented qualifying corrections completed | All qualifying cases and all eligible consumers separately | Detection rate can increase after a useful intervention |
This dictionary distinguishes primary policy-level effects from conditional operational diagnostics. A firm's policy count can rise without an increase in exposed people insured. Written premium reflects booked contract value under applicable accounting conventions; earned premium recognizes exposure over time and does not measure welfare. The number of claims paid differs from the amount paid and from the financial adequacy of each payment. A study should document exposure time, product terms, monetary units, and claim accounting conventions.
Protection under uncertainty and household costs
A useful consumer-centered accounting identity over a specified horizon is
C = P + L - B + F,
where P is premiums attributable to the horizon, L is total measured loss or expense within the defined risk domain, B is insurance benefits received or consistently accrued, and F is included transaction or financing cost. The sign of B reflects its role in reducing net consumer burden. This identity is an analytical accounting convention, not a universal welfare function. It requires aligned cash-flow and valuation dates, clear scope for non-financial losses, and avoidance of double counting benefits paid directly to suppliers.
Insurance protects against states of the world rather than merely reducing average cost. Suppose a low-premium contract costs $300, retains the first $2,000 of a covered loss, and has a $10,000 applicable limit on insurer payment. A higher-premium alternative costs $500, retains $500, and has an otherwise identical applicable limit. Without a loss the first household saves $200. With a covered $1,500 loss, the first pays $1,800 including premium, while the second pays $1,000 including premium and retained loss, assuming the second pays $1,000 in benefits. Other terms are held fixed. These hypothetical scenarios demonstrate that the rank ordering of realized costs depends on the loss state and available liquidity.
Expected consumer welfare may be represented by expected utility of consumption or resources under an explicitly specified distribution of losses and policy benefits. A certainty equivalent can summarize such a model only when preferences, wealth, and probabilities are specified and credibly estimated. Observed policy choices cannot in general identify risk aversion separately from advice, information, liquidity, provider preferences, and restricted product access. For this reason, the trial should report observable protection and financial burden directly and present modeled welfare, if used, with transparent assumptions and sensitivity analysis.
Avoid using premium reductions as savings if the intervention simultaneously reduces benefit scope. For every cost comparison, assess changes in exclusions, limits, deductible, provider network, renewal terms, and risk classification. If predicted costs are used, state the model and prediction date, validate calibration on independent data when feasible, and distinguish prediction errors from observed payments. The Medicare result cited above illustrates the difference between a forecast and an experienced outcome.
Claims selection and competing risks
A claim is observed only after a loss, recognition of possible coverage, decision to notify, and successful recording. Advice can influence each stage. Better advice might increase legitimate notifications by explaining coverage, reduce losses through risk-control guidance, or redirect consumers toward policies with broader insured events. The denominator of claimants is then post-treatment. A decline in the fraction of denied claims might reflect changes in reporting or product composition rather than a causal improvement in claims administration.
Measure all-customer outcomes such as incidence of unresolved material loss, total benefit received per assigned household, and time exposed without cover, complemented by conditional claim-process measures. If the research objective is settlement service among comparable claims, consider a separate randomization of claims assistance after notification or a clearly identified conditional estimand. Specify all eligibility dates before interpreting claim-level comparisons.
Claims unresolved at study end are right-censored if the event of interest is settlement. Closure without payment, withdrawal, and disputed denial may be competing events rather than simply censored observations. Administrative end-of-study censoring and loss of follow-up require distinct handling. Rare severe events need longer follow-up, larger sample sizes, or a descriptive safety surveillance program; an early trial may lack power even if its comprehension endpoint is well estimated.
Persistence, redress, and distributional consequences
Policy lapse may represent affordability pressure, transfer to another insurer, removal of an exposure, or deliberate risk retention. Link renewal and cancellation records to customer-reported or appropriately authorized administrative information. Classify unknown reasons as unknown rather than assuming all lapses indicate harm. For a multi-year investment product, early surrender costs, suitability at the time of sale, and the reasons for changes in household circumstances are all relevant.
The FCA insurance outcomes monitoring review (2024) examined reporting from 20 larger insurance firms. It identified weaknesses in outcome-oriented management information and highlighted the importance of investigating group disparities and tracking the effects of corrective actions. This is supervisory observational evidence, not a randomized estimate. An experimental study can operationalize those concerns by specifying follow-up, independent outcome adjudication, and group-specific safety monitoring before data are examined.
Report absolute levels and absolute contrasts by pre-specified customer groups, such as those needing language assistance, customers with limited liquidity, new entrants, and relevant accessibility needs, where collection and analysis are lawful. A favorable average may coexist with deterioration among a group facing the largest losses from errors. Small subgroup results should carry uncertainty and privacy protection; lack of statistical significance does not establish equality. In a scale decision, consider whether practical harm can be mitigated and whether further evidence is required for a group rather than imposing a uniform conclusion.
International Implementation and Supervisory Permissions
Different regulatory objects and common experimental questions
International comparisons require a stable research object without assuming identical legal definitions. The IAIS Insurance Core Principles provide internationally oriented supervisory standards. Domestic regimes determine who may give advice, which products and disclosures are subject to particular duties, who is accountable, and what permissions apply to research and data use.
In the European Union, the IDD defines a shared legislative baseline and member states implement it nationally. Different national rules and supervisory practices affect channel and experiment design. The EIOPA third IDD report release (2026) describes divergent improvements and weaknesses in advice and selling methods and continuing structural change among intermediaries. This makes site and country characteristics important components of research design rather than mere nuisance variables.
In the United Kingdom, the FCA's Consumer Duty monitoring and communication materials provide specific supervisory context for regulated retail business. A test of a disclosure change should be aligned with the applicable product and conduct obligations; the review documents guide the measurement of understanding and downstream outcomes. The supervisory expectations do not determine which statistical estimator a researcher must use.
In the United States, the NAIC annuity best-interest standard summarizes the 2020 revision to Model Regulation 275. Model provisions do not have uniform binding force solely because the NAIC adopted them. An annuity advice study must identify applicable state enactments, product and producer licensing, and any other relevant state or federal rules. Medicare plan-choice evidence concerns the U.S. health insurance context and cannot establish the legal requirements for commercial annuity advice.
In India, life-insurance experiments illuminate the role of agent remuneration and recommendation behavior. Their publication period and institutional setting matter: the experimental results do not establish current Indian insurance distribution law. Before conducting a modern trial there, verify contemporary producer rules, product categories, and regulatory permissions directly with the relevant authorities.
An international study may additionally include Australia, Canada, emerging inclusive-insurance settings, or other markets once their actual rules and local permissions are established. The present study does not certify the operative law of those additional markets. Its international design is transferable through protocol adaptation, not by treating the EU, UK, or U.S. framework as a global legal rule.
Supervisory and organizational permission
Before field implementation, the investigators should establish the sponsor's authority and the regulatory status of the treatment. A protocol should identify each legal entity, licensed actor, jurisdiction, product, eligibility population, data controller or equivalent role, approved baseline process, and reviewer responsible for the consumer-protection assessment. Where a regulator or institutional ethics body requires notification, authorization, or review, secure it before recruitment. A sandbox, if available and relevant, operates only under its specific terms.
The insurer or broker must have operational capacity to remediate identified harm. A scientific trial should not rely on a later publication to initiate necessary customer protection. Record responsibilities for product oversight, independent advice review, escalation, incident reporting, supplier coordination, and complaints. Ensure that a consumer can exercise normal service rights without having to remain in the research sample.
Cross-border data integration requires separate scrutiny. An identifier linking advice to insurer and claims records may be essential for outcomes but creates re-identification risk. Minimize direct identifiers, maintain a controlled linkage service, use role-based permissions, document data retention and deletion, and select an appropriate lawful basis for each transfer. Pseudonymization reduces exposure but does not by itself make records anonymous. Contractual or regulatory obligations may require retention of some source records independent of the research dataset.
Site comparability and transportability
Replicate definitions of recommendation, encounter, assignment, product universe, and outcome timing across sites. Preserve local distinctions where required by contract or law. For instance, a deductible expressed in local currency can be compared within a country, but affordability is better represented as a proportion of available resources or under a pre-specified standardized scenario. Exchange-rate conversion alone cannot reconcile different benefits, public insurance entitlements, or cost distributions.
Estimate effects by site or pre-defined institutional group where sample size permits. A pooled effect should specify its weights: equal weighting of sites answers a different question from weighting by eligible customers. Generalization to a new jurisdiction requires a target population, overlap in observable effect modifiers, and plausible transportability assumptions. Reweighting cannot create evidence about a channel, population, or product absent from the trial.
The World Bank's Global Findex 2025 overview offers comparative background on adult financial services and resilience. Such household-level context may help frame recruitment, accessibility, and financial constraints; it does not measure the effectiveness of a named insurance adviser or directly identify adequate in-force policies. International market statistics should be used for context and denominator discipline rather than causal claims.
Causal Estimation, Missingness and Replication
Analysis specification and inference
Record the estimand and analysis plan before observing comparative outcomes. Specify the eligible cohort, time zero, outcome window, outcome construction, treatment assignments, strata, clustering, baseline covariates, missing-data handling, multiplicity, and reporting conventions. Freeze the analysis dataset or retain an immutable versioned extract before confirmatory analysis. Any later change belongs in a dated amendment that distinguishes exploratory work.
For a binary outcome, a transparent primary measure is the absolute risk difference between allocated groups. In a hypothetical individually weighted trial, the observed rates 0.68 and 0.60 imply a difference of 0.08, or eight percentage points, and a relative ratio of approximately 1.13. These are illustrative rates, not empirical estimates. An analysis should report denominators and confidence intervals. With cluster assignment, a variance method and randomization scheme appropriate to the cluster level are required; individual-level binomial intervals would ordinarily understate uncertainty.
A regression-adjusted estimate can incorporate pre-specified prognostic baseline covariates and stratification indicators to improve precision. Avoid conditioning on post-treatment variables such as advice receipt, elapsed consultation length, purchase, or reviewer correction in the primary total-effect estimate. With few clusters, consider design-based randomization inference for a specified null and valid finite-sample methods. For effects heterogeneous across units, the inference method must match the estimand and null hypothesis rather than assume that every individual effect is identical.
If cluster sizes differ, define whether the target is the average customer effect or the average cluster effect. A customer-weighted analysis gives greater weight to large clusters. A cluster-weighted analysis treats a small branch and a large branch equally. Informative cluster size, recruitment after randomization, and differential retention can affect both the target and estimation. Report the weighting rule rather than letting software defaults determine the scientific question.
Treatment receipt and instrumental variables
Angrist, Imbens, and Rubin (1996) establish a framework for interpreting instrumental-variable causal effects for compliers under identifying assumptions. For binary assignment and receipt, the Wald ratio is
LATE = [E(Y | Z=1) - E(Y | Z=0)] / [E(D | Z=1) - E(D | Z=0)].
With randomized assignment, relevance, a suitable exclusion restriction, monotonicity, consistency, and the assumed interference structure, the ratio identifies a local average treatment effect for compliers. It is undefined when the first-stage difference is zero. A weak first stage makes inference unstable. If a tool offer produces a hypothetical eight-percentage-point outcome gain and increases receipt by 0.40, the arithmetic ratio is 0.20; the causal interpretation is justified only by the assumptions, not by the division.
In insurance advice, exclusion is especially demanding. Sending an invitation may draw attention to renewal even when the tool is not opened. An adviser prompt can affect tone, conversation length, or product comparison beyond the intended checklist. If those paths affect outcomes, assignment is not an instrument that operates solely through the coded exposure. The intention-to-treat result remains the more credible policy measure when randomization is intact.
Quasi-experimental evaluation
Randomization may be infeasible for a regulator-wide rule, a natural change in remuneration, or a new platform introduced across an insurer's entire network. A design must then justify a comparison independent of the outcome-generating process. A before-after change combines intervention effects with market movements, product repricing, seasonality, regulatory changes, and selection into the customer population.
Difference-in-differences uses the change in a treated group relative to the change in a suitable comparison group. Its identifying premise is the relevant parallel-trends condition in untreated potential outcomes, with no anticipation or other disqualifying interference under the specified design. Calendar-time graphs, baseline cohort comparability, and clear documentation of other reforms improve credibility but cannot prove the counterfactual assumption.
Callaway and Sant'Anna (2021) develop difference-in-differences with multiple time periods for varying treatment adoption dates under appropriate assumptions. When insurance branches adopt software at different times, estimate group-time effects using eligible comparison cohorts, document whether controls are never treated or not yet treated, and transparently aggregate. A conventional two-way fixed-effects coefficient can obscure heterogeneous dynamics if already treated units become comparisons under staggered adoption. Adoption timing selected in response to poor recent outcomes poses a further threat.
A regression discontinuity design may exploit a genuinely enforced eligibility cutoff, such as an independently assigned threshold that triggers enhanced review. The effect pertains to consumers near the cutoff, and manipulation, simultaneous thresholds, or discontinuous underlying risk can invalidate it. A matched observational comparison can reduce measured imbalance but depends on conditional exchangeability; unobserved consumer preferences and adviser selection remain important threats. Neither design acquires experimental validity from technical complexity.
Attrition and partial identification
Outcome absence is a scientific finding about the observation process. Report the number assigned, the number with administrative records, attempted contacts, successful follow-ups, exposure exits, missing records, and reasons by arm. Distinguish impossible-to-observe outcomes from genuine zero events and from observed non-enrollment. An absent claim record is not necessarily evidence of no loss.
For a binary endpoint, let a be the fraction of assigned consumers with observed outcomes and r the success fraction among observed consumers. Without restrictions on missing outcomes, the population success probability is bounded by [ar, ar + (1-a)]. In a hypothetical enhanced arm with 90 percent observed and 70 percent successes among observed, the bounds are [0.63, 0.73]. For a comparison arm with 95 percent observed and 62 percent successes, they are [0.589, 0.639]. Subtracting worst-case limits gives effect bounds from -0.009 to 0.141, before sampling uncertainty. Thus an observed positive contrast is compatible with a small negative population effect. All values are hypothetical.
Lee's (2009) work on sample-selection bounds offers a more structured approach under monotonic selection assumptions. When one group has higher observation probability and monotonicity is justified, trimming the appropriate extreme outcomes from that group can bound a treatment effect in an always-observed subpopulation. For example, observation rates of 0.95 and 0.90 imply trimming approximately (0.95-0.90)/0.95 = 0.0526 of the observed higher-retention distribution, subject to the directional assumptions and the appropriate handling of ties. This is distinct from the unrestricted bounds above and targets a different population.
Inverse-probability weighting or multiple imputation may help when conditional missingness assumptions are defensible and there is sufficient overlap. Include predictors of missingness that are measured appropriately and avoid creating treatment leakage through model development. Neither method substitutes for retaining the eligible frame or collecting follow-up. Report sensitivity to plausible departures from the assumed missingness mechanism and incorporate appropriate clustering.
Multiplicity, heterogeneity, and adverse outcomes
A design has one or a small set of primary questions. If ten outcomes are tested independently at a nominal five percent level under a global null, the probability of at least one rejection is approximately 1-0.95^10, or 40.1 percent. Real outcomes are correlated, so this illustrative figure does not give the actual familywise probability in a specific study. It demonstrates the need to distinguish confirmatory endpoints from exploratory measures, pre-specify multiplicity handling, and report all tested outcomes.
Heterogeneity analysis should use pre-treatment characteristics and formally evaluate interactions rather than comparing significance in one subgroup with nonsignificance in another. A subgroup-specific interval may remain wide when the overall effect is precise. Report the number of customers and clusters contributing to each subgroup. Safety evaluation should retain serious individual-event review even when confirmatory multiplicity procedures are applied to efficacy endpoints.
Equity evaluation must identify the relevant opportunity or harm. Equal recommendation acceptance across groups is not necessarily equitable when needs differ. A difference in denial rates can reflect case mix, coverage composition, access to the claims process, or discrimination. A trial can estimate the effect of a defined intervention on a group-specific outcome, but it should avoid inferring the cause of all historical disparities from that contrast alone.
Worked protocol for an enhanced needs discussion
The following protocol is a hypothetical example of research design, not a trial that has been registered, authorized, or executed.
The target population consists of adult retail property-policy renewal customers with a continuing insured exposure, served by participating branches in one lawful jurisdiction. The baseline workflow is a documented compliant renewal discussion with normal disclosures and service access. The treatment adds a structured prompt about loss exposure and capacity to meet the retained loss, a plain-language comparison of two or more feasible deductible options when available, and an independent review of material mismatches before binding. Both arms preserve all mandatory disclosures and allow adviser overrides consistent with the law.
Randomize branches in strata based on prior renewal volume and baseline coverage-quality audits, using an independent allocation script. Before allocation, record branch eligibility and the customer-frame construction. Recruit consecutive eligible customers without regard to anticipated acceptance. The primary outcome is an independently adjudicated appropriate coverage state at day 180, using a rubric set before assignment. Consumers who verifiably exit the exposure are handled under a specified outcome strategy; report the exposure-exit count separately. Secondary endpoints cover comprehension shortly after advice, major recommendation errors, coverage-gap days, premium and retained-loss exposure, complaints, correction, and renewal persistence. Real claim frequency and amounts are monitored as longer-term exploratory or safety measures unless sample size and follow-up support a confirmatory analysis.
The illustrative power calculation suggests 31 retained clusters per arm under the stated assumptions. Recruit at least 45 customers per retained cluster for approximately 40 evaluated participants, with a design-specific adjustment for variable sizes and whole-cluster dropout. Store a randomization receipt, baseline roster, protocol version, advice version, and timestamps for data linkage. An independent customer-protection officer resolves serious incidents regardless of assignment. Follow-up is conducted through a common administrative process and a separately consented survey if required.
The primary analysis estimates the customer-average assignment effect, with weights appropriate to the recruitment design and cluster-aware inference. Report unadjusted and pre-specified adjusted estimates, observation probabilities, and unrestricted missing-outcome bounds. Sensitivity analyses examine alternative definitions of affordable retained loss, exposure exit, and disputed adjudication. Exploratory subgroup interactions address baseline liquidity constraints and customer accessibility needs. Track advisers changing branches, product repricing, competing interventions, and evidence of contamination.
Archive the analysis code, machine-readable data dictionary, synthetic test fixtures, output tables, allocation metadata as permitted, and the protocol and amendments. Publish aggregate results that protect confidentiality; share restricted data only through an authorized access process. The study is considered scientifically reported when investigators disclose assignment, actual delivery, observation, uncertainty, adverse events, and whether the primary endpoint and safety criteria support adoption.
Replication and implementation decisions
Replication is an independent test of a specified causal contrast in a new sample or context. Re-running an analysis on the same data tests computational reproducibility. Both are necessary for a mature evidence program, but they answer different questions. A second site may replicate the protocol with local product terms, while retaining the same functional endpoint definitions. If treatment versions differ, describe the common elements and the differences before pooling results.
An implementation decision should compare incremental research and operating cost with observed protection benefits, subgroup outcomes, service capacity, and credible adverse-event monitoring. The analysis may report the incremental cost per additional customer with appropriate protection when the outcome effect is positive and cost accounting is comparable. The ratio is unstable near a zero effect, so show its components and uncertainty. It is not a universal monetary value of protection.
Evaluate scaling separately because an intervention effective in a small study may change adviser behavior, queue length, or product availability when introduced throughout a market. A supervisor can use evidence from several designs: standardized encounters to identify procedural problems, a randomized comparison to assess an enhancement, and ongoing surveillance to evaluate durability or unintended substitution. Causal research and routine monitoring are complementary forms of evidence.
Conclusion
The scientific evaluation of insurance advice requires an explicit counterfactual linked to the actual risk-transfer decision. The proper treatment is a specified change in the advice process; the proper comparison is a credible, legally permissible alternative; and the proper outcome depends on a pre-defined relationship between the consumer's exposure and contractual protection.
The analysis establishes several methodological conclusions. First, assignment and receipt are separate events; the intention-to-treat estimate generally provides the most direct measure of a distribution policy's effect. Second, adviser learning, organizational communication, and shared information produce contamination and require deliberate allocation and variance design. Third, independent suitability adjudication and direct comprehension assessment measure different aspects of quality. Fourth, longitudinal protection requires outcomes defined over all eligible consumers, including those who decline or discontinue insurance. Claim-level indicators remain valuable operational diagnostics but can be selected by the intervention itself. Fifth, international comparison must preserve local legal and institutional distinctions.
The author's synthesis connects experimental identification with insurance-specific exposure accounting and consumer protection. It shows why a single sales, satisfaction, or premium measure cannot establish that advice improves the economic consequences of insurance. A recommendation procedure should be assessed through its effects on appropriate choices, coverage continuity, financial burden, and serious consumer harms, within a documented institutional and causal framework. These conclusions are analytical applications of established research methods. No new named theory, validated universal measurement scale, or newly estimated empirical treatment effect is claimed.
References
Anagol, Santosh, Shawn Cole, and Shayak Sarkar. 2017. Understanding the Advice of Commissions-Motivated Agents: Evidence from the Indian Life Insurance Market. The Review of Economics and Statistics 99(1): 1-15. DOI: 10.1162/REST_a_00625. Publisher abstract.
Kling, Jeffrey R., Sendhil Mullainathan, Eldar Shafir, Lee C. Vermeulen, and Marian V. Wrobel. 2012. Comparison Friction: Experimental Evidence from Medicare Drug Plans. Quarterly Journal of Economics 127(1): 199-235. DOI: 10.1093/qje/qjr055. Publisher abstract.
Bundorf, M. Kate, Maria Polyakova, and Ming Tai-Seale. 2019. How Do Humans Interact with Algorithms? Experimental Evidence from Health Insurance. Stanford Institute for Economic Policy Research working-paper summary; June 2019. Working-paper summary.
European Parliament and Council. 2016. Directive (EU) 2016/97 on insurance distribution, Article 20: Advice, and standards for sales where no advice is given. EIOPA Single Rulebook, updated July 5, 2024. Article 20.
European Parliament and Council. 2016. Directive (EU) 2016/97 on insurance distribution, Article 30: Assessment of suitability and appropriateness and reporting to customers. EIOPA Single Rulebook. Article 30.
European Insurance and Occupational Pensions Authority (EIOPA). 2025. EIOPA Publishes the Results of the First Coordinated Mystery Shopping Exercise in the EU's Insurance Sector. June 17, 2025. Official results release.
European Insurance and Occupational Pensions Authority (EIOPA). 2026. EIOPA Publishes Third Report on the Application of the Insurance Distribution Directive. March 30, 2026. Official report release.
Financial Conduct Authority (FCA). 2024. Insurance Multi-Firm Review of Outcomes Monitoring under the Consumer Duty. June 26, 2024. Supervisory review.
Financial Conduct Authority (FCA). 2026. Consumer Understanding: Good Practice and Areas for Improvement. Supervisory publication, March 2026. Supervisory review.
International Association of Insurance Supervisors (IAIS). 2024. Insurance Core Principles and Common Framework for the Supervision of Internationally Active Insurance Groups. ICP and ComFrame Online Tool. ICP online tool.
National Association of Insurance Commissioners (NAIC). n.d. Annuity Suitability and Best Interest Standard. Insurance Topics. Accessed November 19, 2026. Model regulation overview.
National Commission for the Protection of Human Subjects of Biomedical and Behavioral Research. 1979. The Belmont Report: Ethical Principles and Guidelines for the Protection of Human Subjects of Research. U.S. Department of Health, Education, and Welfare. HHS online edition. Official report.
Campbell, Marion K., Gilda Piaggio, Diana R. Elbourne, and Douglas G. Altman, for the CONSORT Group. 2012. Consort 2010 Statement: Extension to Cluster Randomised Trials. BMJ 345:e5661. DOI: 10.1136/bmj.e5661. Institutional publication record and abstract. Institutional record.
Hudgens, Michael G., and M. Elizabeth Halloran. 2008. Toward Causal Inference with Interference. Journal of the American Statistical Association 103(482): 832-842. DOI: 10.1198/016214508000000292. Published article PDF, alternate host. Published article PDF.
Angrist, Joshua D., Guido W. Imbens, and Donald B. Rubin. 1996. Identification of Causal Effects Using Instrumental Variables. Journal of the American Statistical Association 91(434): 444-455. DOI: 10.1080/01621459.1996.10476902. Accessible author version: NBER Technical Paper 136 (1993), DOI: 10.3386/t0136. NBER author version.
Callaway, Brantly, and Pedro H. C. Sant'Anna. 2021. Difference-in-Differences with Multiple Time Periods. Journal of Econometrics 225(2): 200-230. DOI: 10.1016/j.jeconom.2020.12.001. Accessible author preprint (2018), arXiv:1803.09015. Author preprint.
Lee, David S. 2009. Training, Wages, and Sample Selection: Estimating Sharp Bounds on Treatment Effects. Review of Economic Studies 76(3): 1071-1102. DOI: 10.1111/j.1467-937X.2009.00536.x. Institutional publication record and abstract. Institutional record.
World Bank. 2025. The Global Findex Database 2025. Washington, DC: World Bank. Report overview. Official report overview.