Developing Adaptive Interventions for Cocaine Cessation and Relapse Prevention: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Developing Adaptive Interventions for Cocaine Cessation and Relapse Prevention (NCT02896712), a randomized phase 2 study. The primary outcome is Cocaine Use as Assessed by Proportion of Visits (Excluding Excused Absences) With Cocaine-negative Urine Drug Screen.

2. Clinical Question

The registry describes a staged research question rather than a single treatment comparison. First, the investigators aimed to assess whether ACT with CM increased initial response. They then planned to examine dopamine-targeted pharmacotherapy as an augmentation strategy for people who did not respond, and compare ongoing behavioral approaches for people who did respond. These later questions concern different parts of the adaptive treatment pathway and should not be collapsed into the primary comparison.

The posted primary outcome concerns the initial phase and is based on urine drug screens. The registry also reports secondary measures of cocaine-free days over 4 weeks and 12 weeks. Those outcomes offer related but not identical views of cocaine use: one is based on visits and urine results, while the others use Timeline Follow-back reports of days without cocaine use. The record does not report a single overall estimate for the complete adaptive sequence.

3. Trial Design

This is a Phase 2, randomized, parallel-group trial listed as completed. The registry reports enrollment of 118 and identifies cocaine-related disorders as the condition under study. The sponsor is The University of Texas Health Science Center, Houston. The recorded study start was 2016-11-18, and primary completion was 2021-09-13.

The initial comparison assigned participants to ACT plus CM or DC plus CM. ACT was described as aiming to decrease experiential avoidance and increase acceptance and willingness to experience unpleasant thoughts, feelings, and physical symptoms. DC was described as providing education about concepts in addiction recovery. CM was used with each behavioral approach. The record lists quadruple masking, but does not report which specific roles were masked or how masking was maintained.

The adaptive plan had additional treatment branches. For nonresponders to initial treatment, the investigators planned to examine pharmacotherapy augmentation. For responders, they planned to assess continued ACT plus CM against DC plus CM for relapse prevention. The listed phase-two options include ACT plus CM or DC plus CM, each with placebo or modafinil augmentation; some descriptions also list behavioral treatment without augmentation. The medication descriptions specify modafinil 300mg capsules and identify weeks 5-12 as the phase-two period for augmentation.

The primary endpoint is reported for the Phase 1 groups. The posted results include group means and standard deviations, alongside an unadjusted mean-difference estimate. The registry does not report a statistical analysis for the full adaptive decision strategy, the randomization details within each phase, or the original design assumptions used to plan enrollment. Those details are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Phase 1

Phase 2

Analysis population for the primary outcome, as defined in the registry: Using a modified intention-to-treat plan, data are reported for all participants who completed at least one visit after randomization.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Cocaine Use as Assessed by Proportion of Visits (Excluding Excused Absences) With Cocaine-negative Urine Drug Screen, measured over 4 weeks.

The primary endpoint is the mean proportion of visits, excluding excused absences, with a cocaine-negative urine drug screen over 4 weeks. Urine is assessed for benzoylecgonine (BE), a cocaine metabolite; the screen is considered positive for cocaine use when BE is ≥ 150 ng/mL. A negative screen therefore contributes to the outcome as a visit without a positive cocaine screen.

This measure is used because it relies on an objective urine test at study visits, rather than solely on participant report. Expressing the outcome as a proportion of visits gives a continuous measure that summarizes the share of assessed visits with a negative screen. It does not represent the proportion of all calendar days without cocaine use, and it does not count excused absences as observed negative screens.

The primary population is defined using a modified intention-to-treat plan: data are reported for participants who completed at least one visit after randomization. Thus, the endpoint does not include every randomized participant regardless of follow-up. The registry does not report the handling of missing urine results beyond this population description, nor does it report a separate endpoint estimate for participants with no post-randomization visit.

7. Results Posted in the Registry

• Phase 1: DC Plus CM: mean 0.24 versus 0.31 on control; difference -0.07 (95% CI -0.20 to 0.06), standardized effect d = -0.20; z-test p = 0.295.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Cocaine Use as Indicated by Proportion of Days of no Cocaine Use as Assessed by Timeline Follow-back

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Phase 1: DC Plus CM: mean 0.66 versus 0.70 on control; difference -0.04 (95% CI -0.13 to 0.05), standardized effect d = -0.16; z-test p = 0.402.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Phase 1: DC Plus CM and the control. The interval gives the range of effects that remain compatible with the data.

Cocaine Use as Assessed by Proportion of Days of no Cocaine Use as Assessed by Timeline Follow-back

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • ACT Plus CM: mean 0.83 versus 0.58 on control; difference 0.25 (95% CI 0.09 to 0.41), standardized effect d = 1.04; z-test p = 0.002.
  • ACT Plus CM, With Modafinil: mean 0.70 versus 0.58 on control; difference 0.12 (95% CI -0.04 to 0.28), standardized effect d = 0.49; z-test p = 0.152.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for ACT Plus CM than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ACT Plus CM, With Modafinil and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the picture by measuring cocaine-free days through Timeline Follow-back, alongside the primary endpoint’s urine-screen-based measure of visits. The 4-week secondary measure is conceptually closer in timing to the primary endpoint, while the 12-week measure addresses a longer assessment period and includes phase-two treatment groups. Agreement across measures could strengthen confidence that a pattern is not specific to one measurement approach, while disagreement could reflect differences in timing, data collection, or the populations represented.

Across the posted summaries, the early comparison does not show a clear separation between the behavioral groups on either the primary visit-based measure or the 4-week self-reported day measure. The 12-week summaries vary across treatment options. This broader pattern should be viewed as descriptive rather than as a single estimate of the adaptive strategy: phase-two groups arise from different treatment pathways, and their means are not all estimates of the same contrast.

Unadjusted secondary results carry less weight for confirmatory interpretation when multiple outcomes and comparisons are examined. Without a reported multiplicity plan, the chance of at least one apparently notable result across several comparisons is not controlled by considering each p-value in isolation. The registry lists no reported analyses for these outcomes, and no multiplicity adjustment is reported. Secondary patterns can help identify questions for further study, but should not be treated as independent confirmation of the primary result or as proof about the whole adaptive sequence.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Cocaine Use as Indicated by Proportion of Days of no Cocaine Use as Assessed by Timeline Follow-back
• Cocaine Use as Assessed by Proportion of Days of no Cocaine Use as Assessed by Timeline Follow-back

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean represent? The primary measure is continuous because it is a proportion summarized across participants. A group mean describes the average observed proportion of visits with negative urine screens in that group. It does not mean every participant had that exact proportion, and it does not describe how many participants met a binary response definition. The standard deviation describes the spread of individual values around the group mean. A larger standard deviation indicates more variability in the observed values, not greater uncertainty in the treatment contrast by itself.

What does a mean difference express? A mean difference subtracts one group mean from another. The primary comparison is oriented as DC plus CM minus ACT plus CM, so a negative estimate corresponds to a lower mean in the DC plus CM group. Its sign depends on the order of subtraction; it is not a direction-free measure of effect. The reported estimate is unadjusted and does not account for covariates or other features of the study design.

How should the p-value be read? A p-value describes how unusual data at least as incompatible with a specified null comparison would be under the assumptions of a statistical test. It is not the probability that the null hypothesis is true, nor is it a measure of the size or clinical importance of a difference. The primary p-value is unadjusted. Because the registry lists no reported analyses, the test model and any prespecified inferential procedure are not reported in the registry record. The recalculated comparison is therefore best treated as a simple reading of the posted summary statistics.

What does the confidence interval add? A confidence interval expresses the uncertainty around an estimate under the method used to construct it. It gives a range of values compatible with the data and method, rather than a range containing a stated proportion of individual participant outcomes. When an interval for a difference includes zero, the data do not clearly distinguish the observed contrast from no difference under that interval procedure. This does not prove equality. The width also matters: a broad interval leaves more uncertainty about the size and direction of the underlying contrast than a narrow one.

Why can proportions vary? Participants may differ in their patterns of use, attendance, and observed urine results. A proportion-of-visits measure can also be influenced by how many visits each participant completes. Excluding excused absences defines which visits contribute to the endpoint, but the record does not give a complete missing-visit model. General statistical reasoning suggests that uneven follow-up or missing outcome measurements can affect both the estimated group means and their uncertainty; the direction of any such effect cannot be inferred without further information.

Why distinguish description from analysis? The registry reports arm-level means and standard deviations and allows a straightforward unadjusted comparison to be calculated from them. Such a calculation does not reproduce an analysis that might account for repeated measures, stratification, baseline values, or the adaptive sequence. The registry record does not report whether or how any such methods were used. No model-specific assumptions should be attributed to the investigators on the basis of the posted summaries alone.

What does over-dispersion mean in general? In general, over-dispersion occurs when outcome variability is greater than a statistical model expects. A model that underestimates variability can make uncertainty intervals too narrow and significance assessments too optimistic. The primary outcome is reported as a mean and standard deviation, and the registry does not identify a model or report an over-dispersion assessment. This is a general concept, not a claim that over-dispersion was present in this trial.

How do the adaptive phases affect interpretation? An adaptive trial can address different questions among participants who follow different response pathways. An initial comparison, a medication-augmentation comparison among nonresponders, and a relapse-prevention comparison among responders have different target populations and contrasts. An analysis of one branch cannot automatically be interpreted as an estimate for the entire strategy. The registry describes these intended questions and lists several phase-two groups, but does not report an analysis combining the branches or estimating the value of the overall decision strategy.

What is the status of the posted inferential results? No reported analyses are listed for the primary or secondary outcomes. Accordingly, the effect estimates and p-values discussed in the statistical reading are unadjusted recalculations from posted summaries, not reported adjusted analyses. The record does not state the original statistical plan, the handling of interim looks, or a sample-size justification for the trial. These omissions limit how far the reported summaries can be interpreted as confirmatory evidence.

11. Confidence Intervals and Precision

The primary mean difference is -0.07, with a confidence interval that extends from -0.201 to 0.061. Because the interval crosses zero, the posted summary does not rule out no difference under the interval method. It also includes values on either side of zero, so the direction of the underlying contrast remains uncertain. The interval is more informative than the point estimate alone because it conveys the range of estimates compatible with the observed data and calculation method.

The interval should not be read as showing that the treatment effects are equally likely at every point within it, or as describing the distribution of individual outcomes. It also does not account for any multiplicity adjustment. The registry does not report a sponsor analysis or the interval-construction procedure, so the interval associated with the simple unadjusted recalculation should be interpreted with that limitation.

Precision is affected by the amount of observed variability and the information available in the groups. The primary standard deviations are 0.36 and 0.34, indicating substantial spread in participant-level proportions relative to the scale of the means. The posted group sizes are 53.0 and 57.0. These features help explain why a point estimate should not be treated as exact, but they do not alone establish whether a difference is meaningful.

The interval and p-value address statistical uncertainty, not the importance of a difference to participants or clinicians. A small p-value, if present, would not by itself establish importance; conversely, an interval that includes zero does not demonstrate equivalence. The registry does not report an equivalence margin or a threshold for a clinically important change.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total participants, for the comparisons shown. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its starting point and considers planning for 100%, 75%, or 50% of that observed effect. These are planning illustrations, not the trial’s original sample-size assumptions; those original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the stated calculation would require to have an 80% chance of detecting the chosen effect, under its assumptions and if that effect were the true effect. The 90% power column makes the corresponding calculation for a 90% chance. A higher target probability generally requires more participants for the same effect. Planning for a smaller effect also requires more participants, as the columns for reduced fractions of the observed effect illustrate.

These counts are not a retrospective measure of the probability that this completed trial found a result, and they do not say whether the trial was adequately planned. They are not observed power. The calculation is based on the observed effect, which is uncertain, and its assumptions may not reflect the original design or analysis. In general, a curve translating effect size into required participants is a way to see how planning requirements change as the target effect becomes smaller or larger; it is not evidence about the result itself.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.070; pooled standard deviation σ = 0.350.
2. n = 2 × (1.96 + 0.842)² × 0.350² / -0.070² = 391.9, rounded up to 392 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.07                      # observed difference in means
sigma <- 0.349772412778282                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2896712)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 392 (80% power), 525 (90% power)
 75% of observed effect: n per arm = 697 (80% power), 933 (90% power)
 50% of observed effect: n per arm = 1,568 (80% power), 2,099 (90% power)
power.t.test: 392.9 
Simulated power at n = 392 per arm: 0.804 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The record lists four outcome measures and multiple comparisons across the initial and later treatment phases. It does not report a hierarchy of hypotheses, a family-wise error strategy, a false-discovery approach, or another multiplicity adjustment. It also does not report which outcomes or comparisons were designated confirmatory beyond identifying the primary outcome. As a result, unadjusted p-values should be interpreted cautiously when considered alongside several secondary outcomes and treatment contrasts.

The registry lists no reported analyses for the primary or secondary outcomes. The original statistical analysis plan, including any planned covariate adjustment, repeated-measures method, interim analyses, or rules for evaluating the adaptive branches, is not reported in the registry record. The absence of a reported analysis is not evidence that no analysis was conducted; it means that the registry entry does not document one. The simple unadjusted recalculations from the posted summaries do not resolve these missing details.

The primary population is described as modified intention-to-treat and includes participants who completed at least one post-randomization visit. That definition makes the analysis population narrower than all randomized participants. The registry does not describe how missing urine tests, missed visits, or incomplete Timeline Follow-back data were handled, whether imputation was used, or whether sensitivity analyses were performed. It also does not report the number excluded from each outcome because of missing data.

These gaps matter because missingness and multiplicity can affect both uncertainty and the interpretation of findings. If the probability of having an observed outcome differs by treatment or by participants’ outcomes, complete-case summaries may not represent the randomized groups in the same way. The available record does not establish whether that occurred. Likewise, without a documented multiplicity plan, a notable secondary comparison cannot be interpreted as though it were the only comparison tested.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: suicidal ideation (10.0%), asthma attack (5.0%), upper respiratory infection (5.0%), symptoms of congestive heart failure (5.0%), domestic violence/abuse (1.9%).

The serious adverse event summaries give the number at risk and the number affected within each listed phase and treatment group. In Phase 1, the record lists 3 serious adverse events among 54 at risk for ACT plus CM, and 1 among 64 at risk for DC plus CM. In the phase-two groups, the listed serious-event counts range from 0 to 3, with group-specific numbers at risk ranging from 10 to 23. There were 0 deaths recorded in every listed group.

These are group-level counts, not estimates adjusted for exposure time or differences in follow-up. The phase-two groups are not interchangeable with the initial groups, and the record does not provide a statistical comparison of adverse-event rates. Serious-event terms listed include suicidal ideation, asthma attack, upper respiratory infection, symptoms of congestive heart failure, domestic violence/abuse, and stomach flu. The recorded percentages attached to those terms should be read as descriptive registry entries, not as evidence of a causal treatment relationship.

Absence of a recorded death or a low event count does not establish that an intervention is safe. The registry summaries do not provide enough detail to assess event timing, severity beyond the serious-event classification, attribution, or comparative risk.

16. What the Result Does, and Does Not, Mean

The posted primary results describe the average proportion of observed visits with negative cocaine urine screens in two initial behavioral-treatment groups. The unadjusted contrast is modest in the reported units, and its confidence interval includes zero. The available summary therefore does not provide clear statistical evidence of a difference between those groups on this endpoint. It also does not establish that the approaches are equivalent or that any difference is unimportant.

The measure is limited to visits during the stated 4-week timeframe and excludes excused absences. It reflects urine-screen status at observed visits, not continuous abstinence, all days without cocaine use, or longer-term relapse prevention. The secondary Timeline Follow-back outcomes address reported days without cocaine use, but they do not turn the primary result into a measure of the entire adaptive care pathway.

The trial’s stated purpose spans initial response, augmentation for initial nonresponders, and relapse prevention among responders. The primary comparison addresses only the initial groups. Phase-two summaries concern different options and populations, and the registry does not report an analysis of the complete adaptive strategy. Conclusions about one phase should not be generalized to every treatment choice in the study.

The result also does not establish that ACT, DC, CM, placebo, or modafinil caused a particular outcome. The posted estimates are group summaries and unadjusted recalculations; the registry record does not include a reported inferential analysis or the original analysis plan. Statistical uncertainty, the outcome definition, missing-data details, and multiple comparisons all constrain interpretation.

In practical terms, the record documents a randomized study and reports outcomes, but the primary estimate is not precise enough to distinguish a clear difference from no difference under its interval calculation. It is a limited finding about the posted data, not a recommendation about treatment and not a general claim about effectiveness.

17. Why This Trial Matters Statistically

This trial raises a statistical question that is central to adaptive intervention research: how should evidence be interpreted when treatment choices and target populations change according to earlier response? An initial randomized comparison, a later augmentation question, and a relapse-prevention question are related, but they are not the same estimand. Clear reporting needs to distinguish each branch and explain how the branches contribute to any overall strategy estimate.

The primary endpoint also illustrates the importance of defining the measurement process. A proportion of visits with a negative urine screen is not interchangeable with days without reported use. It depends on observed visits, excludes excused absences, and is restricted to participants with at least one post-randomization visit under the stated population plan. The secondary Timeline Follow-back outcomes provide another perspective, but differences in measure and timeframe need to remain visible.

Finally, transparent reporting of analysis plans, missing-data handling, and multiplicity is particularly important when a study has several outcomes and treatment pathways. The registry record identifies the clinical questions and gives descriptive summaries, yet does not report analyses for the listed outcomes. That distinction helps readers separate what the record documents from what would be needed for a full statistical evaluation of the adaptive strategy.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the detailed randomization procedure, allocation concealment, or the identities of the roles included in quadruple masking. It describes the design labels but does not give enough detail to assess how these features were implemented. The original sample-size justification and design assumptions are also not reported; the planning illustrations based on observed effects should not be mistaken for the trial’s own design calculations.

The primary endpoint population excludes randomized participants who did not complete a post-randomization visit. The record does not describe missing-outcome handling or provide sensitivity analyses. This limits assessment of how complete-case summaries may relate to outcomes among all randomized participants. The registry also does not report baseline characteristics or adjusted estimates in the outcome record.

Interpretation of phase-two summaries is limited by the different response pathways, the small group-level counts shown for some treatment options, and the absence of reported inferential analyses. The record does not provide a combined analysis of the adaptive treatment strategy or a documented multiplicity approach. Adverse-event summaries are descriptive and do not include comparative statistical analyses or event attribution details.

These limitations do not invalidate the posted summaries, but they restrict conclusions that can be drawn from them. The registry record offers a view of the recorded outcomes, not a complete account of trial conduct or the investigators’ full statistical analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Developing Adaptive Interventions for Cocaine Cessation and Relapse Prevention — NCT02896712.
• Registry record last updated 2023-02-08; status last verified 2023-01.
• Results first posted 2023-02-08.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02896712 is a completed Phase 2 randomized parallel-group study of adaptive interventions for cocaine cessation and relapse prevention, sponsored by The University of Texas Health Science Center, Houston. The study enrolled 118 and compared ACT plus CM with DC plus CM in the initial phase, with later treatment options involving placebo or modafinil augmentation.

The primary outcome was the mean proportion of visits with cocaine-negative urine screens over 4 weeks, among participants with at least one post-randomization visit. The posted initial-group means were 0.31 and 0.24; the unadjusted mean difference was -0.07, with a confidence interval spanning zero and an unadjusted p-value of 0.295. The registry lists secondary cocaine-use measures and adverse-event counts, but no reported analyses for the outcomes. The full analysis plan and missing-data methods are not reported in the registry record.