Culturally-Tailored Approach to Improve Medication Use in Patients With Heart Attacks: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Culturally-Tailored Approach to Improve Medication Use in Patients With Heart Attacks (NCT00426231), a randomized na study. The primary outcome is Achievement of LDL-cholesterol Goals.

2. Clinical Question

The trial addresses a practical question about whether hospital-based support can affect a measurable aspect of medication-related care after a heart attack. The registry describes several potential barriers to statin use, including affordability, prescribing after discharge, and cultural mistrust. The intervention was designed to address those issues through counseling and assistance accessing pharmacy programs.

The primary endpoint is achievement of an LDL cholesterol level below 100 mg/dL at 6 months. It is a binary outcome: each participant is classified according to whether the recorded LDL result meets the stated goal. The posted comparison estimates the difference between groups in the proportion meeting that goal. A separate secondary outcome concerns self-reported medication adherence at 6 months, which captures a different aspect of medication use.

The record describes follow-up at baseline and at 6 and 12 months, with an additional visit at 24 months for participants enrolled during the early recruitment phase. The posted primary results concern the 6-month endpoint; results for other time points are not reported in the registry record. The trial does not, in these results, directly answer every question about statin use, later clinical events, or the cost of running the program.

3. Trial Design

The registry identifies this as a randomized, parallel-group trial with no masking. Participants were assigned to the Patient Navigator Intervention or Information Control. The registry lists enrollment as 140, while the posted primary outcome denominators are 36.0 in the intervention group and 37.0 in the information control group. The reason those figures differ is not reported in the registry record, so the enrollment entry should not be treated as the denominator for this particular outcome comparison.

The sponsor is Johns Hopkins University. The registry lists the study start as 2006-03, primary completion as 2009-12, and status as completed. The listed conditions are coronary arteriosclerosis and myocardial infarction. The phase is recorded as NA, which is the registry classification rather than a description of a drug-development phase. The trial compares a behavioral intervention with an information control; it is not described as a comparison of two statin regimens.

The planned program was hospital-based and culturally tailored. The brief description says that a community health worker would counsel patients and help with pharmacy assistance programs. The registry gives short arm descriptions, but does not report detailed implementation procedures, the content of the information control, or how consistently the intervention was delivered.

Outcomes were intended to be assessed at baseline and at follow-up. The primary endpoint reported in the results is achievement of the LDL-cholesterol goal at 6 months. The primary endpoint description says that, for an intention-to-treat analysis, the randomization-visit status is carried forward when 6-month data are missing. The registry does not report the number of missing results or a complete participant flow for the posted outcome.

The record lists one secondary outcome, self-reported medication adherence, also assessed at 6 months. It describes an additional visit at 24 months for participants enrolled during the early recruitment phase, but does not report outcome estimates for that visit. The registry does not report the original statistical plan, the rationale for the enrollment target, or detailed randomization procedures.

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.

Before assignment: Participants were enrolled during their hospitalization. Participants had their randomization visit at 1 month.

Overall Study

Reasons for not completing this period:

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 Achievement of LDL-cholesterol Goals, measured over 6 months.

The primary endpoint is the number of participants achieving an LDL-cholesterol level below 100 mg/dL at 6 months. The registry describes this as achievement of the LDL-cholesterol goal. It is a binary endpoint: a participant either meets the stated threshold or does not, based on the available LDL measurement and the endpoint’s missing-data rule.

This kind of endpoint is useful when the clinical question concerns how often a prespecified target is reached. It translates each participant’s measurement into a readily interpretable target-attainment outcome and permits a comparison of the proportions meeting the goal in the randomized groups. The posted result therefore describes target achievement, rather than the average LDL level or the size of any change in LDL cholesterol.

The endpoint description specifies that, for intention-to-treat analysis, the randomization-visit status is carried forward if the 6-month follow-up result is missing. That rule means the classification used for a participant with a missing follow-up result is based on the earlier randomization visit rather than a new 6-month measurement. The registry does not report the number of participants whose result was handled this way or the distribution of missingness by group.

Achievement of this laboratory target is not itself a direct measure of medication-taking behavior, cardiovascular events, or program cost. Medication adherence is listed separately as a secondary outcome, and the brief description mentions other planned assessments. Results for those additional outcomes are not reported in the registry record. The primary endpoint should therefore be interpreted specifically as a comparison of LDL-goal attainment at the stated follow-up, not as a complete assessment of every aim described for the study.

7. Results Posted in the Registry

• Patient Navigator Intervention: 86.1% (31/36) versus 78.4% (29/37) on control; risk difference 7.7 percentage points (95% CI -9.7 to 25.2), risk ratio 1.10 (0.89–1.36); unadjusted two-proportion z-test p = 0.388.

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.

Self-reported Medication Adherence

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Patient Navigator Intervention: 44.4% (16/36) versus 51.4% (19/37) on control; risk difference -6.9 percentage points (95% CI -29.8 to 16.0), risk ratio 0.87 (0.53–1.40); unadjusted two-proportion z-test p = 0.555.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Patient Navigator Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome, self-reported medication adherence at 6 months, measures a different domain from the primary LDL-goal endpoint. Its point estimate is in the opposite direction from the primary estimate, while its uncertainty also spans both directions of a group contrast. The overall pattern is therefore not a consistent directional signal across the laboratory target and the self-reported behavior measure.

This divergence does not resolve the primary comparison. The two outcomes are related by the study’s broad aim of improving medication use, but they are not interchangeable: a participant’s reported adherence and achievement of a laboratory target are distinct observations. The registry does not provide an analysis connecting individual adherence reports to LDL results, so no participant-level relationship between these measures can be inferred.

The secondary result should carry less weight than a prespecified primary outcome when drawing a focused conclusion. It is an additional comparison, and the record does not report whether the secondary analysis was prespecified in detail, how many analyses were planned, or whether any adjustment for multiple testing was used. Unadjusted secondary results can be more vulnerable to chance findings when multiple outcomes or comparisons are considered. This is a general statistical concern, not evidence that a particular result is false.

The record lists one secondary outcome and does not report secondary analyses in detail. The secondary result can inform the broader interpretation by showing that the medication-use question was considered from a self-report perspective, but it is not a substitute for the primary result and cannot establish an intervention effect on medication use. The absent multiplicity and analysis details limit how confirmatory the secondary comparison can be considered.

Other outcomes described in the study summary, including follow-up beyond 6 months, imaging, and cost-effectiveness, do not have posted results in the registry record. The secondary pattern should therefore be interpreted as limited to the reported adherence outcome, rather than as a comprehensive account of the trial’s other stated aims.

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

• Self-reported Medication Adherence

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary, because it records whether each participant achieved the LDL-cholesterol goal. For a binary outcome, a group proportion is the number meeting the definition divided by the number assessed for that outcome. The posted group counts and denominators describe the observed outcome data; they should not be confused with the registry’s overall enrollment figure.

What does the risk difference express?

The risk difference compares the outcome proportions in the two groups by subtracting the control-group proportion from the intervention-group proportion. A positive estimate means the observed outcome proportion is higher in the intervention group; a negative estimate means it is lower. Here, the posted primary estimate is positive. The risk difference is expressed on the probability scale, so it describes an absolute contrast rather than a relative ratio. It is an unadjusted comparison: the registry does not report a covariate-adjusted primary estimate.

Risk differences are often useful because they stay close to the outcome as experienced in each group: how much the proportion achieving the target differs. They do not, on their own, explain why the groups differed or whether the difference is attributable to the intervention beyond the protections afforded by randomization and the analysis assumptions. Randomization supports a group comparison, but uncertainty, missing data, and implementation still affect interpretation.

How should the p-value be read?

The unadjusted p-value is a measure of how unusual the observed result, or a result more extreme under the test’s definition, would be if the null comparison and test assumptions held. It is not a measure of the size or clinical importance of the difference. It is not the probability that the intervention has no effect, and it does not establish that the groups are the same. The registry gives an unadjusted p-value but does not report the statistical test or a more detailed analysis specification.

General statistical explanation: a p-value is sensitive to both the estimated contrast and the amount of information in the data. A wide confidence interval can accompany a p-value that does not meet a conventional significance threshold when the observed sample is small or the outcome is variable. The p-value should therefore be considered alongside the estimated difference and its confidence interval rather than treated as a stand-alone conclusion.

What does the confidence interval add?

A confidence interval gives a range of effect estimates compatible with the data under the interval’s statistical procedure. In general, it conveys precision: a narrower interval reflects greater precision, while a wider interval reflects greater uncertainty. The primary interval spans negative and positive risk differences, so the data are compatible with more than one direction of group contrast. The interval does not give the probability that the true effect lies within its particular bounds.

The registry does not state the specific method used to form the posted confidence interval. General statistical explanation: interval calculations for binary outcomes can depend on the estimator and method, especially with limited observations or proportions near the boundaries. The available record does not permit a more specific description of those calculation choices.

What does intention-to-treat mean in this record?

The primary endpoint description refers to intention-to-treat analysis and specifies a rule for missing 6-month observations: the randomization-visit status is carried forward. In general, intention-to-treat analysis aims to compare participants according to their randomized assignment, rather than reassigning them according to later treatment received. The registry does not provide a full analysis-population definition or details about adherence to the assigned program.

Carrying an earlier status forward is a particular approach to missing outcome data. General statistical explanation: such a rule treats the earlier measurement as a stand-in for the unobserved follow-up status. If missingness is related to later outcome status, the resulting comparison may be biased; the direction and size of any bias depend on the missing-data pattern and cannot be determined from the posted information. The number of missing observations and sensitivity analyses are not reported in the registry record.

How should the secondary outcome be considered?

The secondary outcome is self-reported medication adherence, a binary measure reported at the same follow-up. The comparison is likewise an unadjusted risk difference with a confidence interval and p-value. Self-report can reflect recall and reporting as well as medication-taking behavior, so it is conceptually different from a laboratory endpoint. The registry record does not report validation information or a detailed definition of adherence.

General statistical explanation: testing several outcomes can increase the chance of a seemingly notable result arising by chance if each is considered independently. A prespecified hierarchy, adjustment procedure, or clear distinction between confirmatory and exploratory analyses can help frame that issue. Multiplicity handling and the detailed statistical plan are not reported in the registry record, so the secondary result should be interpreted cautiously.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.077, and its 95% confidence interval extends from -0.097 to 0.252. The interval includes zero, meaning that the posted data are compatible with no group difference as well as with differences in either direction under the interval procedure. Its range also includes positive estimates larger than the point estimate. The range is therefore not precise enough to pin down the direction and magnitude of the underlying comparison.

A confidence interval is not a probability statement about the true effect. In general, a 95% confidence procedure is designed so that intervals formed repeatedly under the same method would contain the fixed underlying parameter at the stated long-run rate. For an individual interval, the appropriate reading is about the set of estimates that remain compatible with the data and procedure, not that there is a 95% probability that the true effect is inside the displayed bounds.

The interval’s width reflects uncertainty in the group contrast. The registry reports outcome denominators of 36.0 and 37.0 for the primary comparison. Those denominators are modest for estimating proportions, and the resulting interval is broad. No additional precision should be inferred from the enrollment entry, because the reason for the difference between enrollment and these outcome denominators is not reported in the registry record.

The secondary adherence comparison also has a wide interval that spans zero. It does not materially resolve the uncertainty in the primary result, because it measures a different outcome and is itself imprecise. Nor does the primary interval establish equivalence: a claim of equivalence would require an appropriate prespecified margin and analysis, which are not reported in the registry record.

These intervals describe uncertainty for the posted comparisons, not uncertainty about all outcomes mentioned in the study description. Estimates for 12-month follow-up, the additional 24-month visit, arterial imaging, and cost-effectiveness are not reported in the registry record. The precision of the primary comparison should be judged only for the endpoint and time point actually reported.

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 for 80% power and participants per arm for 90% power. They are not totals across both groups. The registry’s sample-size assumptions describe a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The scenarios use the stated fraction of the observed effect as the effect to detect. Because these outcomes are not time-to-event outcomes, the figures refer to participants per arm, not total events.

Each scenario asks how many participants per arm a future study would need, under those assumptions, to have the stated chance of detecting the selected effect if that effect were real and the assumptions held. The 80% power column represents an 80% chance of detecting that effect under the specified model; the 90% column represents a higher chance of detection and therefore generally requires a larger planned sample. The rows for 100%, 75%, and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects need more participants because they are harder to distinguish from random variation.

The figures are planning illustrations computed from the observed effect, not a reconstruction of the trial’s original design calculation. The original sample-size assumptions and justification are not reported in the registry record. These estimates are not observed power: observed power is not a useful substitute for reading the estimate and its confidence interval after a study is complete. The planning figures also depend on the stated assumptions and should not be read as guarantees about a future study.

The displayed estimates are tied to each outcome’s observed comparison. They should not be treated as a recommendation for a particular study size without considering the target effect, outcome definition, missing-data approach, and design assumptions. The registry does not report whether the original enrollment target was based on these calculations or on a different planning method.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.784; treatment proportion p₁ = 0.861; average p̄ = 0.822.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5404 = 1.0592.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5376 = 0.4525.
4. n = (1.0592 + 0.4525)² / (0.0773)² = 382.2, rounded up to 383 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
p0 <- 0.783783783783784                          # control proportion
p1 <- 0.861111111111111                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(426231)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 383 (80% power), 512 (90% power)
 75% of observed effect: n per arm = 710 (80% power), 949 (90% power)
 50% of observed effect: n per arm = 1,660 (80% power), 2,221 (90% power)
power.prop.test: 382.2 
Simulated power at n = 383 per arm: 0.798 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 registry reports one primary outcome and one secondary outcome in the posted results. It gives an unadjusted comparison for each, but does not report a statistical analysis plan, a testing hierarchy, or a method for controlling multiplicity. Whether any multiplicity adjustment was planned or performed is not reported in the registry record.

General statistical explanation: when several outcomes are tested, the chance of at least one apparently unusual result can rise if each test is judged separately without accounting for the number of tests. Prespecifying one primary endpoint can help focus interpretation, while secondary outcomes may be considered supportive or exploratory depending on the protocol and analysis plan. Here, the registry identifies the LDL-goal measure as primary and adherence as secondary, but does not give enough analysis detail to establish how these designations governed statistical testing.

The primary endpoint description specifies an intention-to-treat approach in which randomization-visit status is carried forward if 6-month data are missing. The number of missing observations, their distribution between groups, and the number affected by this rule are not reported in the registry record. The missing-data strategy for the secondary adherence outcome is also not reported. No sensitivity analyses for missing outcomes are listed.

General statistical explanation: missingness can affect an estimate when the chance of an unavailable result is related to the unobserved outcome. Carrying an earlier status forward makes an explicit assumption about the unavailable follow-up classification, but the record does not provide enough information to assess that assumption. Without missingness counts and sensitivity analyses, the robustness of the comparisons to alternative missing-data approaches cannot be evaluated.

The primary description names intention-to-treat, but a full definition of the analysis population and a participant flow are not reported. The record also does not describe per-protocol or other analysis populations. It is therefore not possible to determine from the registry record how many randomized participants contributed to each analysis beyond the outcome denominators shown or how exclusions and incomplete follow-up were handled overall.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

The registry records zero serious adverse events among the 36 participants at risk in the Patient Navigator Intervention group and among the 37 participants at risk in the Information Control group. It also records zero other adverse events in both groups, using the same group-specific at-risk counts. These are the adverse-event figures posted for the trial.

These counts should be read as registry-reported observations, not as proof that no adverse events occurred outside the recorded definitions or observation period. The adverse-event timeframe, ascertainment procedures, and definitions are not reported in the registry record. Deaths are not reported in the registry record; the death fields are not populated with a count.

The figures do not provide a detailed comparison of event risk or establish that the groups had identical safety experience. The number of participants with recorded events is limited, and zero reported events does not rule out events that were not recorded or uncommon events that the study could not characterize. The record lists no serious adverse-event terms, which is consistent with the zero serious-event counts entered for both groups, but does not supply further narrative about safety monitoring.

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

The posted results show the observed 6-month comparison for achievement of an LDL-cholesterol goal, along with a separate self-reported adherence comparison. The primary point estimate is positive for the patient navigator group, but its confidence interval includes zero and extends in both directions. The unadjusted p-value does not provide evidence of a clearly resolved group difference. Taken together, the estimate and interval indicate uncertainty rather than a precise conclusion about the size or direction of the underlying contrast.

That interpretation is not the same as saying that the intervention had no effect. A result that does not distinguish clearly between groups may reflect a small effect, no effect, or uncertainty arising from limited information; the posted data do not separate those possibilities. Nor do the results establish that the groups are equivalent. The registry record does not report an equivalence margin or an equivalence analysis.

The endpoint measures whether a participant reached the specified LDL threshold, not the average LDL level, adherence verified from pharmacy records, recurrent heart attacks, arterial imaging findings, or cost-effectiveness. The brief description identifies those broader interests, but results for them are not reported in the registry record. The secondary adherence outcome is self-reported and should not be treated as direct confirmation of medication use.

The missing-data rule for the primary endpoint carries forward the randomization-visit status when 6-month data are unavailable. Without the number and pattern of missing results, it is not possible to assess how much that rule influences the estimate. The registry also does not report detailed intervention fidelity, statistical modeling choices, or adjustment for multiple comparisons.

Accordingly, the results are best read as a limited comparison of the recorded outcomes at the reported follow-up. They neither demonstrate a reliable benefit nor establish a lack of benefit. They also do not answer whether the program changes later clinical outcomes or whether it is cost-effective. Those questions require outcome information and analyses that are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates a targeted, binary outcome from the broader claims that might be attached to a medication-support program. The primary measure asks whether participants met a defined LDL-cholesterol threshold at 6 months. The posted risk difference puts the group contrast on an absolute probability scale, while its confidence interval makes the uncertainty in that contrast visible.

The estimate is not interpreted in isolation. Its interval spans zero, and the unadjusted p-value does not resolve the comparison. This illustrates a central principle of trial interpretation: the data can be compatible with a range of effects even when a single point estimate appears to favor one group. Reading the estimate, interval, outcome definition, and missing-data rule together is more informative than reducing the result to a significance label.

The trial also shows why outcome domains matter. LDL-goal attainment is a laboratory target; self-reported adherence is a behavioral report. A result in one does not automatically validate or negate the other. Their differing point-estimate directions make it especially important not to collapse them into a single claim about medication use.

Finally, registry results need to be considered in light of what is not documented. The record does not report the original sample-size justification, detailed analysis plan, multiplicity handling, or missingness pattern. Those omissions limit the ability to evaluate design choices and robustness. Distinguishing recorded evidence from unreported details is an important part of statistical interpretation, particularly when a trial’s stated aims extend beyond the outcomes with posted estimates.

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.

Several limitations are specific to the information recorded for this trial. Although enrollment is listed as 140, the primary outcome denominators are 36.0 and 37.0. The registry does not explain the relationship between those entries or provide a complete participant flow. The reason for the difference should not be inferred from the available record.

The trial is described as randomized and unmasked, but details of sequence generation, allocation concealment, implementation, and the content of the Information Control are not reported in the registry record. The intervention is described as involving a community health worker, counseling, and help with pharmacy assistance programs, but implementation fidelity and uptake are not reported. These omissions restrict assessment of how consistently the intervention was delivered and what the contrast between groups involved in practice.

The primary endpoint is reported at 6 months, with a specified carry-forward rule for missing primary outcomes. The count and pattern of missing observations are not reported, and no sensitivity analysis is listed. The registry does not give a detailed statistical analysis plan, test specification, or multiplicity procedure. It also does not report results for the other follow-up visits or for imaging and cost-effectiveness aims described in the study summary.

The secondary adherence measure is self-reported. The record does not provide a detailed adherence definition or validation information. Safety reporting is limited to group counts; the event observation period and ascertainment procedures are not reported, and deaths are not reported in the registry record.

These record-level limitations do not establish that the underlying study lacked these procedures or data; they mean that those details cannot be evaluated from the registry record. They constrain interpretation of the posted outcome comparisons and the scope of conclusions that can be drawn from them.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Culturally-Tailored Approach to Improve Medication Use in Patients With Heart Attacks — NCT00426231.
• Registry record last updated 2014-02-24; status last verified 2014-01.
• Results first posted 2014-02-24.
• 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

NCT00426231 is a completed randomized, unmasked, parallel-group trial sponsored by Johns Hopkins University. The registry lists enrollment as 140, a start date of 2006-03, and primary completion in 2009-12. The conditions listed are coronary arteriosclerosis and myocardial infarction; the phase is recorded as NA.

The comparison was Patient Navigator Intervention versus Information Control. The primary outcome was achievement of an LDL-cholesterol goal at 6 months, with self-reported medication adherence listed as a secondary outcome at the same follow-up. The primary comparison has a positive risk-difference estimate, but its confidence interval includes zero and its unadjusted p-value does not resolve the group contrast. The secondary estimate is also uncertain.

The primary endpoint description specifies carrying forward randomization-visit status when 6-month data are missing. The original sample-size rationale, detailed analysis plan, missing-data counts, and results for other follow-up visits and broader study aims are not reported in the registry record.