Reproducible Reporting of Marketing Technology Experiments: A Protocol for Experimental Design, Data Generation, and Field-Study Documentation

1. Introduction and research question

Marketing technology experiments are now used to test advertising claims, influencer messages, sponsorship disclosures, and direct-marketing interventions in settings that range from short online exposure tasks to naturalistic field designs. This protocol examines what would be required to report assignment logic, exposure delivery, outcome construction and data handling consistently; it does not estimate the prevalence of reporting omissions. The research question guiding this protocol is: what minimum reporting structure would allow a third party to reconstruct the experimental logic of a marketing technology study, rerun its analysis pipeline on the same data, and compare it with other studies that manipulate digital marketing exposure? The answer proposed here is a reporting protocol rather than a new empirical model. It is designed for experiments in which a marketing message, claim, or promotional format is assigned to units such as people, households, sessions, impressions, or events, and in which outcomes include perception, preference, intention, engagement, or behavior.

The evidence scope is a targeted narrative synthesis of methodological problems visible in recent direct applications. Studies of emojis in marketing report that the field is heterogeneous in theory and method, with many experiments using simple designs and relatively little field experimentation, which constrains ecological validity [Vardikou et al.]. Influencer marketing research in tourism commonly uses cross-sectional survey designs with latent-variable modeling, but the same literature also emphasizes trust, content quality, and audience segmentation as operational constructs that should be recorded precisely when interventions are tested [Babu et al.]. In contrast, experimental and field-experimental studies in adjacent marketing domains show how causal inference depends on transparent assignment, timed exposure, and outcome windows: counter-advertising around alcohol sponsorship used pretest-posttest measurement around a real sporting event [Dixon et al.], and a gambling direct-marketing study used stratified randomization with ecological momentary assessment to reduce recall bias [Rockloff et al.]. These studies do not solve the reproducibility problem, but they reveal where reporting is often strongest and where it is still incomplete. [1] [2] [3] [4]

2. Evidence scope and analytic orientation

This manuscript does not attempt a systematic review. Instead, it uses a targeted narrative synthesis to identify recurring reporting requirements across marketing technology experiments and to convert those requirements into a reproducible protocol. The synthesis prioritizes studies that test how marketing interventions are delivered and measured, rather than broad marketing theory. Four design patterns are especially relevant. First, a literature review on emojis in marketing notes that experiments often use the marketing cue as an independent variable, but report weak coverage of advertising settings and field experiments [Vardikou et al.]. Second, the influencer marketing tourism study provides a typical example of survey-based measurement of perceived influence, but its structure also clarifies how operational indicators are usually grouped into constructs such as trust, emotional connection, and content quality [Babu et al.]. Third, the alcohol sponsorship counter-advertising experiment demonstrates how pretest exposure, time-bounded intervention delivery, and event-linked follow-up can be reported in a way that preserves causal interpretation [Dixon et al.]. Fourth, the gambling marketing field experiment shows the value of stratified allocation, proof of intervention compliance, and repeated outcome measurement in a naturalistic context [Rockloff et al.]. [1] [2] [3] [4]

The analytic orientation of the protocol is deliberately conservative. It assumes that reproducibility in this domain depends less on a single statistical estimator than on complete reporting of the treatment chain: what was assigned, to whom, when, through which platform, under what eligibility rules, with what outcome window, and with what preprocessing rules. The protocol therefore treats reproducibility as a property of the full study object, not only of the final model. This is important because the same marketing intervention can generate different estimands depending on whether the unit is a user, an impression, a session, or a household, and because exposure can be measured at the intended, delivered, or received level. Without explicit distinctions among these levels, apparently comparable studies may actually estimate different causal quantities.

3. Core reporting principles

The protocol defines four reporting principles. First, the experimental unit must be declared before data analysis begins. If a platform randomizes by user account but the analytic file contains repeated sessions, the report should state that user account is the randomized unit and session is the observation unit. Second, treatment specification must distinguish message content from delivery mechanism. For example, a claim framed as a health assertion, a product claim, or a social proof cue should be coded separately from the channel used to display it. Third, all derived variables must be traceable to raw events by a documented transformation chain. Fourth, every deviation from the assigned exposure must be reported as an implementation event rather than hidden in the cleaning stage.

The exact operational rule for exposure classification is as follows: a unit is classified as exposed only if the predefined intervention was delivered and the platform log shows at least one viewable impression within the prespecified observation window; otherwise the unit is classified as assigned-but-not-exposed. This rule separates assignment from delivery and prevents post hoc redefinition of treatment status. If a study uses multiple exposures, then cumulative exposure should be defined as the count of qualifying impressions within the window, and the threshold for “received dose” must be stated in advance. Any alternative rule, such as click-based exposure, should be justified as a distinct estimand rather than treated as equivalent.

4. Proposed methodology for reproducible marketing technology experiments

The proposed methodology has six components. Component one is a preregistered design matrix. For each experimental factor, the investigator records the factor name, allowed levels, unit of randomization, and expected direction of effect if any directional claim is made. Component two is a standardized intervention dictionary. Each treatment condition receives a machine-readable code that maps to message text, visual assets, targeting criteria, platform, timing, and exclusion rules. Component three is a data-generation log. This log records the source of each raw field, timestamp format, missingness code, and any platform-level throttling or suppression rule. Component four is a comparator specification. The default comparator is the closest plausible counterfactual: no claim, neutral claim, placebo-like content, or business-as-usual marketing, depending on the setting. Component five is a predeclared outcome set. Primary outcomes should be measured on the closest causal path to the intervention: recall, credibility, intention, click-through, conversion, dwell time, or behavioral choice. Secondary outcomes may include sentiment, trust, or brand awareness, but they should not be substituted for the primary endpoint after inspection of results. Component six is a reproducible analysis script that ingests the raw data and exports the analysis-ready dataset with versioned metadata. [2] [3] [4]

Operational definitions should be explicit enough to survive platform change. For advertising-claim experiments, a claim is any message element that asserts product attribute, superiority, scarcity, healthfulness, or social approval. For influencer experiments, the treatment is not merely “influencer content” but a coded bundle containing creator type, disclosure status, message authenticity cues, and content format. For field tests of marketing effects, the primary implementation variable is exposure opportunity, not only reported recall. The protocol recommends recording at least four outcome layers: message reception, immediate cognitive appraisal, behavioral intention, and observed behavior. If observed behavior is unavailable, the report must state why and should not infer behavior from intention without qualification. [2] [3] [4]

The decision sequence is as follows. Step 1: define the unit and eligibility criteria. Step 2: assign treatment using a documented randomization or allocation rule, with blocking or stratification when sample heterogeneity is expected. Step 3: deliver the intervention through a logged platform process. Step 4: verify compliance by matching assignment records to impression or receipt records. Step 5: construct primary outcomes using preregistered rules. Step 6: estimate treatment effects using the prespecified model and report any deviations. Step 7: archive all code, metadata, and a data dictionary with version identifiers. This sequence is transferable across laboratory, online, and field settings because it distinguishes causal assignment from technical delivery and from post-treatment measurement. [3] [4]

5. Comparison with prior methods in direct application studies

The proposed protocol addresses three reporting questions illustrated by the selected applications; it does not establish how common each practice is across the field. In emoji marketing research, experimental designs are common, but the review notes that attention has concentrated on short-term outcomes and that field experiments are underrepresented [Vardikou et al.]. The protocol responds by requiring explicit documentation of the outcome window, implementation level, and exposure verification so that short-term engagement studies and longer field studies can be compared on a shared reporting basis. In the influencer marketing tourism study, the emphasis is on modeling relationships among trust, content quality, and purchase intention, using questionnaire items and structural modeling [Babu et al.]. That approach is suitable for explanatory survey work, but it does not by itself define how a promotional message should be delivered and logged. The present protocol adds intervention-level reporting so that future experiments can test the same constructs under controlled exposure conditions. [1] [2]

The alcohol sponsorship counter-advertising experiment illustrates a different design from the cross-sectional survey example because it includes pretest timing, repeated exposure, and event-linked follow-up [Dixon et al.]. The present protocol retains these strengths but formalizes them into a portable reporting structure. In particular, it requires a clear statement of whether the comparator is neutral content, alternative content, or no exposure at all, because this choice changes interpretation. Likewise, the gambling direct-marketing experiment shows the value of stratified allocation, proof of opt-out compliance, and ecological momentary assessment to shorten recall intervals [Rockloff et al.]. The proposed protocol generalizes this logic by requiring compliance verification for any intervention whose receipt can diverge from assignment, including ad-blocked impressions, skipped influencer posts, or platform-delivered claims that never become viewable. [3] [4]

A further difference concerns measurement hierarchy. Prior studies often report either attitudinal outcomes or behavioral outcomes, but not always the chain connecting them. The protocol asks authors to label each outcome as proximal, intermediate, or distal relative to the intervention. This distinction matters because a field experiment that changes awareness but not behavior is still informative, whereas a report that mixes these levels without labeling can overstate inference. The protocol therefore does not mandate a specific statistical model; it mandates a reporting architecture that keeps measurement levels distinct.

6. Validation design for the reporting protocol

Because the present article is a protocol, validation is prospective rather than empirical. The recommended validation design has three stages. Stage one is internal completeness testing. A sample of study reports should be reviewed for whether each record can be reconstructed from the manuscript, appendix, and code archive alone. The criterion is binary at the field level: either the report contains enough information to recover the treatment assignment, outcome definitions, and preprocessing steps, or it does not. Stage two is cross-study comparability testing. Independent coders should map two or more studies to the same template and assess whether the same intervention, comparator, and outcome labels are used consistently. Stage three is reproducibility testing. A second analyst should rerun the supplied code on the preserved raw or synthetic demonstration data and verify that the outputs match the archived tables, figures, and model specifications.

The protocol also recommends a failure analysis. If reproduction fails, the report should classify the cause into one of four categories: missing specification, platform drift, undocumented preprocessing, or ambiguous outcome construction. These categories are not exhaustive, but they help isolate whether a failure arises from incomplete reporting or from genuine platform instability. Where data privacy prevents release of raw data, a synthetic demonstration dataset with the same schema should be provided so that the analysis pipeline can still be executed end to end. This is especially relevant in marketing settings where platform logs, customer identifiers, or proprietary assets cannot be fully disclosed.

Boundary conditions should also be tested prospectively. The protocol may be less suitable for studies in which intervention delivery cannot be logged at the unit level, or where the treatment is so diffuse that exposure is only plausibly measured at the population level. It may also require adaptation for qualitative or mixed-method designs in which the primary evidence is interpretive rather than causal. Those limits should be stated in the protocol itself rather than discovered only after attempted reproduction.

7. Failure cases, limits of generalization, and reporting requirements

The main failure case is conflation of assignment with exposure. In digital marketing, platform rules, ad blockers, skips, privacy settings, and timing mismatches can produce an assignment record without a received treatment. If that distinction is not reported, effect estimates may be misinterpreted. A second failure case is outcome drift, where the study claims to measure one construct, such as purchase intention, but the instrument or behavioral proxy actually captures a different construct, such as general engagement. A third is platform drift, in which the same marketing artifact is delivered differently across operating systems, interface updates, or regional policies. Because the protocol is intended to be transferable across domains, it does not assume stable platform behavior; instead, it requires platform versioning and delivery logging as part of the report.

Generalization should be bounded rather than presumed. The evidence base reviewed here spans advertising claims, influencer communication, emojis, sponsorship counter-advertising, and direct marketing, but these interventions differ in social meaning and in the degree to which they can be isolated experimentally. The protocol therefore generalizes only at the level of reporting structure, not at the level of substantive effect direction. For example, a claim that increased engagement in one context may not do so in another, and a trust cue in influencer marketing may not operate like a promotional claim in a display ad. The protocol can document these differences, but it cannot remove them. [1] [2] [3] [4]

Assignment-preserving reproduction and implementation tests

The primary effect analysis retains randomized units under original assignment. Viewable-impression status is a delivery diagnostic, not a post-randomization eligibility filter; exposed-only effects need separate identification assumptions. Specify viewability using a fixed visible-area threshold, minimum continuous duration, active-tab rule and monotonic clock, with unobservable delivery coded unknown rather than unexposed by default. Repeated observations require uncertainty estimation at the assignment cluster. Choose one primary endpoint and register secondary families and multiplicity rules. Preserve software versions, dependency locks, random seeds, immutable input hashes and expected output tolerances. A privacy-safe synthetic dataset demonstrates executability only: it cannot reproduce the original study’s empirical estimates. Restricted-data reproduction requires an authorized analyst using preserved original data under access controls. Validate this reporting protocol prospectively against independently coded completeness and reproduction outcomes; no adoption benefit or replication success rate is established by the present conceptual proposal.

8. Conclusion

This manuscript establishes a conceptual reporting protocol for reproducible marketing technology experiments. The central proposal is that reproducibility depends on a transparent chain from assignment to delivery, from delivery to outcome construction, and from analysis to archived code and metadata. The protocol offers explicit definitions for the experimental unit, comparator, exposure classification, and outcome hierarchy, and it specifies a validation sequence for checking whether a study can be reconstructed by independent analysts. It also shows how methods used in prior direct applications of digital marketing research can be translated into a more general reporting architecture, especially where studies involve claims, influencer content, counter-advertising, or direct marketing. [1] [2] [3] [4]

What remains untested is whether this protocol measurably improves reproducibility, comparability, or downstream reuse of marketing experiment data in practice. That question requires an empirical evaluation across multiple study types and platform environments. Until such validation is completed, the contribution of this manuscript is limited to a precise and falsifiable reporting framework, not to demonstrated gains in replication success or effect estimation.

References

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