Efficacy and Safety of Imipenem+Cilastatin/Relebactam (MK-7655A) Versus Colistimethate Sodium+Imipenem+Cilastatin in Imipenem-Resistant Bacterial Infection (MK-7655A-013): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Imipenem+Cilastatin/Relebactam (MK-7655A) Versus Colistimethate Sodium+Imipenem+Cilastatin in Imipenem-Resistant Bacterial Infection (MK-7655A-013) (NCT02452047), a randomized phase 3 study. The primary outcome is Percentage of Participants With Favorable Overall Response (FOR).

2. Clinical Question

The registry describes a Phase III comparison in people with imipenem-resistant bacterial infection. An open-label imipenem/cilastatin/relebactam group is also listed for participants with documented imipenem-resistant and colistin-resistant infections; its efficacy data were described as exploratory. The primary comparison is between the two main treatment groups, rather than an estimate that combines all listed groups.

3. Trial Design

The registry describes a Phase III, randomized, double-blind, active-comparator-controlled, parallel-group trial. Its stated enrollment was 50, and its status is completed. Participants were stratified by infection type and randomized to the main imipenem/cilastatin/relebactam regimen or the colistimethate sodium plus imipenem/cilastatin regimen. The study included HABP/VABP, cIAI, and cUTI.

The registry lists a third group receiving open-label imipenem/cilastatin/relebactam for participants with documented imipenem-resistant and colistin-resistant bacterial infections. This group is described separately from the two blinded randomized groups, and its efficacy data were considered exploratory. The primary outcome is reported for Groups 1 and 2. The posted primary results include 21 participants in Group 1 and 10 in Group 2 for that endpoint; these endpoint populations should not be conflated with the registry’s overall enrollment or safety populations.

The intervention and comparator were intravenous regimens with different accompanying drugs. The registry describes dosing every 6 hours for imipenem-based infusions and every 12 hours for colistimethate sodium or its placebo. Duration depended on infection type, with the specified ranges extending from 5 to 21 days for cIAI and cUTI and from 7 to 21 days for HABP or VABP. The available arm descriptions are incomplete at their ends, so further duration details are not reported in the registry record.

The record reports the trial as completed and gives the primary completion date as 2017-09-18. It does not report the trial’s original sample-size justification, the details of any interim analyses, or a full statistical analysis plan. The registry enrollment figure is descriptive; it does not explain how the planned size was chosen or whether recruitment matched an original target.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in Groups 1 and 2 who received ≥1 dose of each trial drug within a given IV treatment regimen, and who had a baseline bacterial pathogen that met inclusion criteria, are included. As per protocol, efficacy data from open-label Group 3 was considered exploratory and not included in the comparative analysis.

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 Percentage of Participants With Favorable Overall Response (FOR), measured over Up to Day 30 (up to 9 days after completing study treatment).

The primary endpoint is the percentage of participants with favorable overall response (FOR), assessed up to Day 30, up to 9 days after completing study treatment. It combines outcomes selected for the primary infection site rather than applying one identical clinical criterion to every participant.

For HABP/VABP, favorable response was defined by survival through Day 28. For cIAI, it required favorable clinical response at Day 28: resolution of pretherapy symptoms without resurgence, no additional antibiotic therapy, and no unplanned surgical or percutaneous drainage procedure. For cUTI, it required both favorable clinical response and microbiological response at early follow-up. The microbiological component was based on sustained eradication of the baseline uropathogen in urine culture.

This endpoint is used to represent an outcome relevant to the different infection sites included in the study. Its strength is that the criteria address survival, clinical status, and microbiological findings where appropriate. Its interpretation also requires care: the composite meaning depends on the participant’s infection type, so a favorable response does not represent exactly the same individual component outcome for every infection. The registry reports the overall percentage for the two main groups and a sponsor analysis of the difference, but does not provide primary results for the open-label group. The primary outcome population included participants who received at least one dose of each trial drug in the regimen and had an eligible baseline pathogen.

7. Results Posted in the Registry

• Group 2: Colistimethate Sodium + Imipenem+Cilastatin: 70.0% (7/10) versus 71.4% (15/21) on control; risk difference -1.4 percentage points (95% CI -35.8 to 32.9), risk ratio 0.98 (0.60–1.60); unadjusted two-proportion z-test p = 0.935.

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.

Percentage of Participants With ≥1 Events of Treatment-Emergent Nephrotoxicity

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group 2: Colistimethate Sodium + Imipenem+Cilastatin: 56.2% (9/16) versus 9.7% (3/31) on control; risk difference 46.6 percentage points (95% CI 20.1 to 73.0), risk ratio 5.81 (1.82–18.52); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Group 2: Colistimethate Sodium + Imipenem+Cilastatin than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Favorable Clinical Response (FCR) at Day 28

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group 2: Colistimethate Sodium + Imipenem+Cilastatin: 40.0% (4/10) versus 71.4% (15/21) on control; risk difference -31.4 percentage points (95% CI -67.4 to 4.6), risk ratio 0.56 (0.25–1.25); unadjusted two-proportion z-test p = 0.093.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 2: Colistimethate Sodium + Imipenem+Cilastatin and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With All-cause Mortality Up to Day 28

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Group 2: Colistimethate Sodium + Imipenem+Cilastatin: 30.0% (3/10) versus 9.5% (2/21) on control; risk difference 20.5 percentage points (95% CI -10.6 to 51.5), risk ratio 3.15 (0.62–15.97); unadjusted two-proportion z-test p = 0.147.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 2: Colistimethate Sodium + Imipenem+Cilastatin and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover safety and additional efficacy-related measures, including nephrotoxicity, favorable clinical response at Day 28, all-cause mortality, clinical response at other assessment times, and microbiological response among cUTI participants. Taken together, they provide a broader descriptive view than the primary endpoint alone. Their estimates do not form a single uniform pattern of precise effects: some group percentages differ notably, while uncertainty remains substantial for several clinical outcomes.

These endpoints complement the primary outcome because they address distinct aspects of clinical response, mortality, microbiological findings, and adverse events. They are not substitutes for the primary FOR comparison, whose definition incorporates infection-specific outcomes. Nor do secondary outcomes establish the primary result in either direction. Their populations, timeframes, and outcome definitions differ, and the registry does not supply participant-level information to connect outcomes across measures.

The secondary analyses carry less inferential weight because several outcomes were examined and the registry does not report a multiplicity adjustment or a complete analysis plan. When many outcomes are tested, the chance of a nominally notable result arising by chance can increase. This is a general statistical concern, not evidence that any particular result is false. The appropriate reading is descriptive and cautious: secondary findings can help identify patterns for further evaluation, but they should not be treated as independent confirmatory evidence without a reported multiplicity strategy and adequate supporting detail.

The nephrotoxicity result includes a sponsor-reported Fisher Exact analysis, while the other listed secondary comparisons have different reporting details. Differences in methods and confidence levels make it especially important not to treat all outcomes as if they shared a common analysis. The registry’s secondary results are best considered alongside the primary estimate and its uncertainty, rather than as a replacement for it.

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

• Percentage of Participants With ≥1 Events of Treatment-Emergent Nephrotoxicity
• Percentage of Participants With Favorable Clinical Response (FCR) at Day 28
• Percentage of Participants With All-cause Mortality Up to Day 28
• Percentage of Participants With FCR on Therapy (OTX)
• Percentage of Participants With FCR at End of Therapy (EOT)
• Percentage of Participants With FCR at EFU
• Percentage of cUTI Participants With Favorable Microbiological Response (FMR) at OTX
• Percentage of cUTI Participants With FMR at EOT

9. Statistical Interpretation

10. Statistical Methods Explained

Binary outcomes such as favorable response and nephrotoxicity are reported as percentages of participants. A percentage gives the share of the analyzed group meeting the specified outcome definition. It is not a measure of how long an outcome took to occur, and it does not by itself indicate how precise the estimate is. Precision is conveyed separately by the confidence interval.

What does a confidence interval express?

General explanation: a confidence interval describes uncertainty around an estimated quantity under the method used to construct it. A wider interval indicates less precision than a narrower interval. For a between-group difference, an interval that includes zero is compatible with no difference as well as with differences in either direction at the confidence level used. It does not assign a probability to the true value, and it should not be read as a range that contains every plausible value with certainty.

The registry gives 95% confidence intervals for the arm-specific primary percentages, but the sponsor’s reported difference uses a 90% confidence interval. These intervals answer related but different questions: one describes uncertainty around each group percentage, while the other describes uncertainty around the reported contrast. The contrast’s confidence level should be kept in view when interpreting its endpoints. Comparing an arm-specific interval with a contrast interval as if they were interchangeable would be misleading.

What is the difference between the reported analysis and the recalculation?

The posted recalculation is a simple unadjusted comparison of the endpoint counts in the two main groups. It reports a risk difference, with Group 2’s observed proportion contrasted against Group 1’s. This calculation does not reproduce any adjustment, stratification, model, or analysis-population choices that might have been used by the sponsor. The registry’s reported primary analysis gives a difference in FOR of -7.3, with a 90% confidence interval from -27.5 to 21.4, and no p-value is posted for that analysis. The unadjusted recalculation has a different estimate and a 95% interval; these are not identical analyses and should not be treated as competing estimates of the exact same procedure.

The re-calculation is based only on posted summary statistics. It can be useful for understanding the scale and uncertainty of a straightforward comparison, but it cannot recover participant-level data or verify the sponsor’s analysis choices. The record indicates no discrepancy flag. That does not establish that every undocumented analysis detail matches the simple recalculation; it only means the record does not flag a discrepancy between the posted analysis and the recalculated comparison.

Why do small groups affect interpretation?

General explanation: estimates based on small groups can be sensitive to the outcome status of individual participants. This often produces broad intervals for percentages and differences. Sparse data can also make some statistical approximations less reliable. A confidence interval that spans a wide range signals that the observed point estimate should not be read as a precise estimate of the underlying effect.

For binary outcomes, a risk difference expresses the difference between the groups’ event proportions on the proportion scale. A value of zero represents equal proportions; positive or negative values indicate which group has the higher observed proportion according to the stated contrast direction. A risk ratio instead compares proportions as a ratio, and an odds ratio compares odds. These measures have different scales and interpretations, so their numeric estimates are not directly interchangeable. The posted primary comparison is expressed as a risk difference.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variation is greater than a statistical model expects. When present, a model that assumes less variation than the data contain may report uncertainty that is too narrow. The registry record does not report an over-dispersion assessment or a model-based adjustment for it. This concept is relevant generally, but there is no basis in the record to claim that over-dispersion occurred in this trial.

The record identifies the primary endpoint as a percentage and gives confidence intervals, but it does not report the method used to calculate those primary intervals or the sponsor’s primary contrast. It also does not report the original statistical analysis plan. These omissions limit the ability to reproduce the sponsor’s analysis from the registry alone.

What do the p-values add?

General explanation: a p-value measures how surprising data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It does not measure the probability that the null hypothesis is true, nor does it describe the size or practical importance of an effect. A p-value also does not replace an estimate and confidence interval.

The sponsor’s primary analysis has no p-value listed in the registry. The unadjusted recalculation gives p = 0.935, but it is not the sponsor’s analysis. Secondary nephrotoxicity results include a Fisher Exact analysis with p = 0.002. Because multiple secondary outcomes are reported and no multiplicity adjustment is described, that p-value should not be treated as if it were the only statistical test conducted.

The registry also posts planning illustrations based on observed effects. These are not results of a new trial and do not revise the uncertainty of the current estimates. Their assumptions are stated separately in the sample-size reading. The trial’s own design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The primary arm-specific estimates have broad 95% confidence intervals: 49.8% to 86.4% for Group 1 and 39.2% to 89.7% for Group 2. These intervals indicate substantial uncertainty around each percentage. The group point estimates, 71.4% and 70.0%, should therefore not be interpreted as highly precise descriptions of the response percentages that would necessarily recur in other samples.

The sponsor’s reported contrast is -7.3 percentage points, with a 90% confidence interval from -27.5 to 21.4. The interval includes zero and extends in both directions, so the data are compatible with a range of possible differences. Its width matters as much as the point estimate: the registry does not provide a narrow interval that pins down the magnitude or direction of the contrast.

The unadjusted recalculation gives a 95% confidence interval from -0.358 to 0.329 around its risk difference estimate of -0.014. This is a separate calculation from the sponsor’s reported contrast, and the confidence levels differ. It likewise indicates considerable uncertainty. General explanation: larger samples usually provide more precise estimates when other design and analysis features are comparable, while small samples commonly yield wider intervals. That general principle does not establish what the result would be in another trial.

Intervals are not a substitute for examining how an endpoint was defined or which participants were analyzed. Here, infection-specific components make the primary response a composite with differing clinical criteria by infection type. The confidence intervals quantify statistical uncertainty in the estimates, not uncertainty about whether the endpoint definition is clinically appropriate or whether results generalize to other populations.

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 events. They are illustrations computed from the observed effect, not the original design justification for this trial. The assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding number for a 90% chance. These are planning targets, not guarantees about a study’s result. Smaller effects need more participants to detect than larger effects, which is why the illustrations increase when the assumed fraction of the observed effect gets smaller.

For example, the planning figures vary across the rows for detecting 100%, 75%, or 50% of the observed effect. Those rows are alternative planning scenarios, not estimates of effects that the current trial actually established. The observed effect is especially uncertain because the trial’s group estimates have broad confidence intervals; a planning illustration based on a noisy estimate inherits that uncertainty.

This is not observed power. Observed power is not a useful replacement for interpreting the estimates and their confidence intervals after a trial. The planning numbers instead show how assumed effect size and desired power relate to the sample size required under the stated calculation assumptions. They do not demonstrate that the completed trial was adequately or inadequately powered, because its original design assumptions are not reported.

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 = 0.714; treatment proportion p₁ = 0.700; average p̄ = 0.707.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6436 = 1.2614.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6435 = 0.5416.
4. n = (1.2614 + 0.5416)² / (-0.0143)² = 15,928.1, rounded up to 15,929 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 <- 0.714285714285714                          # control proportion
p1 <- 0.7                          # 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(2452047)
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 = 15,929 (80% power), 21,323 (90% power)
 75% of observed effect: n per arm = 28,216 (80% power), 37,773 (90% power)
 50% of observed effect: n per arm = 63,257 (80% power), 84,683 (90% power)
power.prop.test: 15928.1 
Simulated power at n = 15,929 per arm: 0.799 (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. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis gives a difference in FOR of -7.3, with a 90% confidence interval from -27.5 to 21.4. It does not list a p-value or a method for that analysis. The arm-specific percentages are 71.4% for Group 1 and 70.0% for Group 2, each with a 95% confidence interval.

A separate simple unadjusted recalculation from the posted summary counts gives a risk difference of -0.014, with a 95% confidence interval from -0.358 to 0.329, and p = 0.935. This recalculation uses a different confidence-interval level and may not reflect the sponsor’s analysis method or population handling. It should be read as a transparent comparison based on the posted counts, not as a correction to the reported result.

The registry does not flag a discrepancy. The sponsor’s analysis remains the formal reported analysis, while the recalculation offers a basic unadjusted view. The available record does not provide enough methodological detail to reconcile every difference between the two presentations or reproduce the sponsor’s estimate exactly.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes and reports multiple analyses. It does not report a multiplicity adjustment, a prespecified hierarchy for testing outcomes, or a complete statistical analysis plan. The record also does not describe whether any outcomes were designated as exploratory before analysis. These details are not reported in the registry record.

General explanation: when multiple hypotheses are tested, the chance of at least one apparently notable result can increase, even if none of the underlying effects is present. Methods such as a prespecified testing hierarchy or adjustment can address this issue, but they alter how results should be interpreted. Because no such approach is described in the registry record, nominal secondary p-values should be treated cautiously and not as confirmatory evidence on their own.

The record provides an efficacy population definition for the primary endpoint: participants in Groups 1 and 2 who received at least one dose of each trial drug in their regimen and had an eligible baseline pathogen. Safety outcome denominators differ from the primary efficacy denominators. The registry does not report a complete account of missing outcome data, the number of participants with unavailable measurements for each endpoint, or the methods used to handle missing data. It is therefore not possible to assess from the record alone whether missingness could have affected the reported percentages.

The record also does not fully describe the analysis populations for every secondary outcome, the handling of protocol deviations, or whether analyses followed an intention-to-treat principle. Those points are not reported in the registry record. They should not be inferred from the endpoint names or from the sample sizes listed for particular analyses.

Without the original statistical plan, it is also unclear which analyses were planned in advance and which may have been added later. This does not invalidate the posted results, but it limits how strongly they can be interpreted as confirmatory. Clear reporting of multiplicity, missing-data handling, and analysis populations would help readers understand the intended scope of inference.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (66.7%), acute abdomen (33.3%), duodenal perforation (33.3%), hepatic haematoma (33.3%), escherichia urinary tract infection (33.3%).

The safety record lists serious adverse events among participants at risk in each group. Group 1 has 4 participants with a serious adverse event among 31 at risk; Group 2 has 5 among 16 at risk; and the open-label Group 3 has 3 among 3 at risk. These are counts in the posted safety groups and should not be combined with the primary efficacy denominators, which are different.

The record also lists other adverse events and deaths separately. The serious-event terms most frequently listed include pneumonia, acute abdomen, duodenal perforation, hepatic haematoma, Escherichia urinary tract infection, and septic shock, with the reported percentages attached to those terms. The registry does not provide enough detail in these summary figures to establish causation or to compare event severity beyond the reported classification.

These data are descriptive. Group sizes are small and unequal, and the open-label group is particularly limited. Raw counts alone do not account for differences in exposure time, participant characteristics, or event ascertainment. No safety conclusion should be drawn from the counts without considering those limitations and the full clinical context. The registry record does not provide a complete narrative for each serious event or a detailed comparative safety analysis.

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

The posted primary results describe favorable overall response in the two main randomized groups and include a sponsor-reported estimate of their difference. The group percentages are similar as point estimates, but the confidence intervals are broad, and the reported difference interval crosses zero. The data therefore do not precisely identify the size or direction of the contrast. The registry result is an estimate with uncertainty, not a definitive statement about what would occur in every setting.

The endpoint combines different criteria according to infection site. It includes survival for HABP/VABP, clinical response for cIAI, and both clinical and microbiological response for cUTI. A percentage with favorable overall response consequently summarizes outcomes that are related but not identical across participants. Interpretation should account for the mixture of infection types and the endpoint’s composite definition.

The secondary outcomes provide additional descriptions of clinical and safety events, but they do not erase the uncertainty in the primary analysis. The registry does not report a multiplicity strategy, full missing-data handling, or the complete analysis populations for all outcomes. These omissions constrain the strength of conclusions that can be drawn from multiple posted results.

The result does not establish that either regimen is superior, equivalent, or non-inferior. The record does not describe a non-inferiority margin or an equivalence framework. It also does not justify conclusions about other infections, populations, treatment settings, or outcomes beyond those recorded. The open-label group’s efficacy was described as exploratory and no primary estimate is posted for it.

These statements concern statistical interpretation of the registry data and are not treatment recommendations. Decisions about care require clinical judgment and information beyond the summary estimates in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why point estimates alone are not enough for interpreting a clinical comparison. The primary group percentages are close, yet the confidence intervals around the estimates and the reported difference remain wide. The data’s precision is therefore central to understanding what the trial can say: the observed responses are known for the analyzed participants, but the magnitude and direction of a broader group difference remain uncertain.

The endpoint also shows a common challenge in studies spanning more than one infection type. A composite can use outcomes relevant to each condition, but the resulting overall percentage has different clinical components across infection groups. That makes the endpoint’s definition and analysis population essential context for interpretation.

The registry record also demonstrates the distinction between a sponsor-reported analysis and a simple recalculation from summary counts. The recalculation is transparent and useful for orientation, but it does not reproduce undocumented analysis choices. Readers need the sponsor’s analysis details, confidence level, and population definition to understand how the formal result was produced.

Finally, secondary outcomes and safety counts can contribute context without serving as decisive proof. Multiple outcomes, small groups, incomplete information about missing data, and unreported multiplicity procedures all affect how strongly results can be interpreted. These are general statistical considerations that apply to the record’s specific reporting gaps; they are not evidence of misconduct or of an unreported analysis choice.

19. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary efficacy comparison includes small groups, and its confidence intervals are broad. This limits precision and makes the point estimates sensitive to the outcomes of individual participants. The registry’s overall enrollment figure should not be mistaken for the primary endpoint sample, whose posted group sizes are smaller.

The study spans several infection types and uses infection-specific components in the primary composite. The record does not report the primary result separately for each infection type, so the overall comparison cannot show whether the pattern was similar across HABP/VABP, cIAI, and cUTI. The open-label group is described as exploratory and has no posted primary efficacy estimate.

The registry does not report the original sample-size justification, a complete statistical analysis plan, interim-analysis details, a multiplicity strategy, or full missing-data handling. It also does not state a non-inferiority margin or an equivalence framework. These absences limit assessment of the intended inferential claims and the robustness of the reported analyses.

The available arm descriptions are truncated, and the record does not provide enough detail to evaluate adherence, exposure duration by participant, or all protocol deviations. Safety summaries are descriptive and do not provide a full account of event timing, exposure, or causal assessment. These limitations are specific to the information recorded and do not establish that the underlying trial materials lack further detail.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Imipenem+Cilastatin/Relebactam (MK-7655A) Versus Colistimethate Sodium+Imipenem+Cilastatin in Imipenem-Resistant Bacterial Infection (MK-7655A-013) — NCT02452047.
• Registry record last updated 2018-10-19; status last verified 2018-10.
• Results first posted 2018-10-19.
• 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.

23. Record Summary

The registry record describes a completed Phase III randomized, double-blind, parallel-group active-comparator trial in imipenem-resistant bacterial infection. The main comparison was intravenous imipenem/cilastatin/relebactam versus colistimethate sodium plus imipenem/cilastatin. A separate open-label group is listed for participants with imipenem-resistant and colistin-resistant infections, with efficacy considered exploratory.

The primary outcome was favorable overall response assessed up to Day 30, with infection-specific definitions. The registry reports arm-specific percentages and a sponsor analysis of the difference for the two main groups. The posted estimates are imprecise, and the record does not report the full statistical plan, original sample-size justification, multiplicity handling, or complete missing-data methods. Secondary efficacy and safety outcomes are also listed; they require cautious interpretation alongside the primary result and its uncertainty.