This page provides an independent statistical analysis and educational interpretation of publicly reported results. ClinicalTrials.gov provides the official trial registry record. Numerical trial results on this page are restricted to the results posted in the ClinicalTrials.gov record; calculations added by Clinical Biostats are labelled as such.
1. Trial at a Glance
This page covers the registry results for SPECS: Safe Pediatric Euglycemia in Cardiac Surgery (NCT00443599), a randomized na study. The primary outcome is Incidence of Nosocomial Infections in the Cardiac ICU.
| Feature | Registry value |
|---|---|
| ClinicalTrials.gov identifier | NCT00443599 |
| Phase | NA |
| Condition | Heart Defects, Congenital, Hyperglycemia |
| Allocation | Randomized |
| Design model | Parallel |
| Masking | None (open label) |
| Enrollment | 989 |
| Arms in the primary outcome | 2 |
| Lead sponsor | Boston Children's Hospital |
| Results posted | Yes |
2. Clinical Question
Population
Children undergoing heart surgery, described in the study summary as young children and critically ill children. The registry reports an enrollment of 989 participants. The primary outcome was measured during each participant’s cardiac ICU stay.
Intervention
Insulin infusion intended to maintain blood glucose at a target concentration of 80-110 mg/dL. The corresponding trial arm is called Tight Glycemic Control.
Comparator
Standard Care, described as insulin administered according to the discretion of the treating clinical team. The registry also refers to this arm as Usual Care.
Primary question
How did the rate of nosocomial infections attributable to the cardiac ICU stay compare between tight glycemic control and standard care? The outcome was reported as infections per 1000 patient days, with infections assessed using CDC-defined criteria.
The trial’s stated rationale was that elevated blood glucose is common in critically ill children, including those having heart surgery, and may accompany poor outcomes and infection risk. The study therefore examined whether maintaining normal blood glucose levels could reduce infections and improve recovery. The primary endpoint directly addresses the infection part of that question. It does not, by itself, represent every aspect of recovery or establish an effect on any other clinical outcome.
The registry lists secondary outcomes that include cardiac index, ICU and hospital stay, duration of endotracheal intubation, mortality, cardiac function, and immune function. Posted secondary results also include mortality at hospital discharge, mortality at 30 days, and a cognitive evaluation at one year of age. These outcomes provide additional descriptive and comparative information, but their presence does not change which outcome was designated primary.
3. Trial Design
SPECS was a randomized, parallel-group trial with no masking. The registry lists an enrollment of 989 and the status as completed. The study start is recorded as 2006-11, and primary completion as 2012-06. The phase is listed as NA. Boston Children's Hospital is the named sponsor.
The two strategies differed in how insulin was used. In the Tight Glycemic Control arm, insulin was infused to target a blood glucose concentration of 80-110 mg/dL. In Standard Care, insulin was infused at the discretion of the treating clinical team. Thus, the comparison is between a specified glucose target and clinician-directed care, not between insulin and a stated no-insulin strategy.
Random allocation is intended to make treatment groups comparable, on average, with respect to factors that could affect outcomes. The registry does not report the allocation sequence method or whether allocation was concealed. No masking means that participants and clinical staff were not masked according to the registry record. The record does not describe any additional steps to limit the effects of knowing the assigned strategy.
The registry reports 490 participants in each arm for the primary infection-rate outcome. The posted denominators vary for some secondary outcomes: hospital-discharge mortality has denominators of 490 and 489, 30-day mortality has 488 and 484, and the one-year cognitive result has 100 and 101. These outcome-specific denominators should be kept in view when reading results; the record does not explain why they differ.
The registry does not report the protocol’s sample-size justification, the planned statistical analysis, interim analyses, or detailed analysis-population definitions. The available sample-size calculations are planning illustrations based on observed effects, not evidence about the trial’s original design or its observed power.
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 gave consent prior to cardiopulmonary bypass (CPB) surgery, randomization occurred perioperatively and initiation of the protocol occurred postoperatively. 9 subjects were removed from the study between the time of randomization and initiation of the protocol (4 for cancellation of CPB , 3 for physician decision, 2 for death).
Overall Study
| Stage | Tight Glycemic Control | Standard Care |
|---|---|---|
| STARTED | 496 | 493 |
| COMPLETED | 490 | 490 |
| NOT COMPLETED | 6 | 3 |
Reasons for not completing this period:
| Reason | Tight Glycemic Control | Standard Care |
|---|---|---|
| Physician Decision | 2 | 1 |
| Death | 1 | 1 |
| Cardiopulmonary bypass canceled | 3 | 1 |
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.
| Characteristic | Unit | Tight Glycemic Control | Standard Care | Total |
|---|---|---|---|---|
| Participants analysed | 490 | 490 | 980 | |
| Age, Categorical: <=18 years | Participants | 490 | 490 | 980 |
| Age, Categorical: Between 18 and 65 years | Participants | 0 | 0 | 0 |
| Age, Categorical: >=65 years | Participants | 0 | 0 | 0 |
| Age, Continuous | months | 4.3 (1.8 to 9.7) | 4.9 (2.3 to 10.8) | 4.6 (2 to 10.2) |
| Sex: Female, Male: Female | Participants | 241 | 217 | 458 |
| Sex: Female, Male: Male | Participants | 249 | 273 | 522 |
| Region of Enrollment: United States | participants | 490 | 490 | 980 |
6. Primary Endpoint
The registry lists the primary outcome as Incidence of Nosocomial Infections in the Cardiac ICU, measured over Measured during participant's ICU stay, a median duration of 3 days..
| Element | Registry entry |
|---|---|
| Result type | Number |
| Measure of spread | not applicable |
| Unit | infections / 1000 pt days |
| Endpoint classification | not reduced to a single comparison |
The primary endpoint is the incidence of nosocomial infections attributable to a participant’s stay in the cardiac ICU. The registry expresses it as infections per 1000 patient days, so it is a rate that relates infection events to time spent at risk in the ICU rather than simply counting participants with at least one infection. The outcome was assessed during the participant’s ICU stay, whose median duration is reported as 3 days.
The registry says infections were determined according to Center for Disease Control-defined criteria and notes that the definitions are extensive. This matters because an infection rate depends on how infections are defined and identified. A consistent definition is intended to make outcome classification comparable between randomized groups. The registry record does not provide a shorter operational definition or the full criteria in the results text.
In general, a rate using patient time can be useful when participants spend different amounts of time under observation or at risk. It allows event frequency to be described in relation to that exposure time. It is not the same as the proportion of participants who experienced an infection, and the two measures should not be treated as interchangeable.
The primary endpoint focuses on infections occurring in the cardiac ICU. It does not directly summarize infection events outside that setting or all dimensions of recovery. Although the trial’s stated purpose also refers to improving recovery, the primary result should be interpreted as evidence about the recorded ICU infection rate, with other recovery-related outcomes considered separately.
7. Why No Re-analysis Is Shown
8. Statistical Interpretation
The posted primary outcome rates are 8.6 infections per 1000 patient days for Tight Glycemic Control and 9.9 infections per 1000 patient days for Standard Care. Each arm has a reported denominator of 490 participants. Descriptively, the posted rate is lower in the tight-control arm. The registry does not provide a confidence interval, p-value, or other inferential comparison for this primary endpoint, and the record marks a two-arm comparison as missing or not estimable for this count outcome. The observed ordering therefore does not, on its own, establish the size or precision of a between-arm effect.
This distinction is important. The rate values describe the observed data, but without a reported comparison interval it is not possible to assess from the registry results how compatible those data are with a range of possible effects. A numerical difference between the displayed rates should not be taken as a measure of certainty. Nor should a lack of a reported primary comparison be mistaken for evidence that the two strategies have identical effects.
The posted secondary results include comparisons for mortality at hospital discharge, mortality at 30 days, and cognitive scores at one year of age. Their confidence intervals include the no-difference value for each reported comparison, and their unadjusted p-values are 0.996, 0.751, and 0.769, respectively. The mortality results are reported as risk differences; the cognitive result is reported as a mean difference. These estimates are imprecise enough that the posted intervals include effects in more than one direction. They do not support a precise conclusion about a difference in these outcomes.
The registry lists no sponsor-reported analyses for these secondary outcomes. The comparisons should therefore be read as unadjusted summaries of the posted group results, rather than as a complete account of any protocol-specified analysis. The record does not state whether the trial used covariate adjustment, a multiplicity procedure, or a prespecified hierarchy for secondary outcomes.
The sample-size illustrations use observed effects to show how large a future study might need to be under stated assumptions. They are not observed power calculations and do not establish what the original trial was designed to detect. In particular, planning from effects near zero can produce very large illustrative sample sizes. Such calculations describe a hypothetical design exercise, not a finding that the study lacked a particular amount of power.
Overall, the primary rates show a modest descriptive ordering in favor of the tight-control arm, but the registry does not report an inferential comparison for that endpoint. The secondary comparisons also do not provide precise evidence of group differences. These points describe the statistical information recorded; they are not treatment recommendations or a judgment about clinical value.
9. Statistical Methods Explained
Outcome scale and comparison. The primary outcome is a count-based rate: infections per 1000 patient days. Rates account for time at risk, which is useful when observation time can differ across participants. In general, a rate comparison needs a statistical model or other method appropriate for event counts and exposure time. Count data can be more variable than a simple model assumes, a feature known generally as over-dispersion. When over-dispersion is present, standard errors from a model that assumes less variability can be too small, making intervals too narrow and tests too optimistic. The registry record does not report the model, dispersion assessment, or inferential method used for the primary endpoint. It also does not post a two-arm estimate or confidence interval for that comparison.
Binary outcomes. Mortality at hospital discharge and mortality at 30 days are binary outcomes: each participant either had the event by the stated assessment or did not. The posted comparisons use risk differences. A risk difference expresses the difference between the event proportions in the two groups, with zero representing equal proportions. In general, a confidence interval gives a range of effects compatible with the data under the method’s assumptions. If that interval includes zero, the data do not rule out no difference at the stated confidence level. This does not prove the groups are equivalent; the interval may also include potentially meaningful differences in either direction.
The hospital-discharge mortality risk difference is 0.0, with a 95% confidence interval from -0.018 to 0.019 and an unadjusted p-value of 0.996. For 30-day mortality, the risk difference is 0.002, with a 95% confidence interval from -0.011 to 0.015 and an unadjusted p-value of 0.751. These are unadjusted comparisons. A p-value measures how unusual data at least as incompatible with a specified no-difference model would be, assuming that model and the test assumptions; it is not the probability that the no-difference model is true.
Continuous outcome. The cognitive evaluation is reported as a mean and standard deviation in each group. The comparison is a mean difference: 0.6 points, with a 95% confidence interval from -3.406 to 4.606 and an unadjusted p-value of 0.769. In general, a mean difference describes the difference between group averages, while the standard deviation describes variation among participants within a group. These quantities answer different questions. The interval for the mean difference includes zero and spans values on either side of it, so the result does not precisely identify a group difference.
Confidence intervals and interpretation. A confidence interval is a measure of statistical uncertainty around an estimate. In general, intervals are more informative than a point estimate alone because they show a range of effect sizes reasonably compatible with the observed data and method. They do not guarantee that the true effect lies within the particular interval, and they do not account for sources of bias that the design or analysis may introduce. The primary infection-rate result lacks a posted interval, so its precision cannot be evaluated in the same way from the registry record.
Unadjusted recalculations. The registry has no sponsor-reported analyses listed for the posted secondary comparisons. The estimates and p-values should be interpreted as unadjusted comparisons based on the posted group summaries, not as a substitute for an unavailable full analysis plan. Such recalculations do not incorporate unreported covariates, stratification, or other design features. If a discrepancy between a sponsor analysis and a recalculation were recorded, the sponsor’s own analysis would take precedence; the registry record does not flag a discrepancy for these results.
Planning illustrations. The sample-size illustrations use the observed effect as a starting point and show hypothetical planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. They state assumptions of a two-sided significance level of 0.05, equal allocation, and a normal approximation. For the binary and continuous outcomes, the results are participants per arm for 80% power and participants per arm for 90% power. They are not observed power, do not describe the original design rationale, and should not be interpreted as the number of participants needed to establish a clinical conclusion. When the observed effect is close to zero, planning to detect that effect can require very large hypothetical samples. The registry does not report whether the original trial used these assumptions.
What is not available. The statistical analysis plan, primary-endpoint model, handling of missing data, analysis populations, interim analyses, and multiplicity strategy are not reported in the registry record. These omissions limit the ability to evaluate whether the posted summaries fully correspond to the trial’s intended analyses. General statistical interpretation can explain what the displayed measures mean, but cannot supply those missing design details.
10. Multiplicity, Missing Data and Analysis Populations
Multiplicity arises when investigators test or estimate effects for several outcomes, time points, or subgroups. In general, the more comparisons considered, the greater the chance of at least one apparently unusual result arising by chance alone. Methods such as a prespecified hierarchy or adjusted significance thresholds can control this concern, but the registry record does not report a multiplicity strategy or a hierarchy among secondary outcomes.
The registry identifies a primary infection endpoint and lists multiple secondary outcomes. Posted secondary comparisons include two mortality assessments and a cognitive score, and their p-values are unadjusted. They should not be read as if each were the sole planned test. The record does not report whether other outcomes were tested in analyses that are not posted, or whether any adjustment was used outside the information available in the registry.
Missing-data handling is also not reported in the registry record. The posted denominators vary by endpoint: the primary infection result reports 490 participants per arm; hospital-discharge mortality reports 490 and 489; 30-day mortality reports 488 and 484; and the cognitive evaluation reports 100 and 101. Those differences indicate that the number contributing to each posted outcome is not identical. The record does not explain the reasons, describe missing observations, or say whether any imputation or sensitivity analysis was used. No particular cause for the different denominators can be inferred from these figures.
The analysis populations are not reported in the registry record. It is therefore unclear from the posted information whether each comparison uses all randomized participants, participants with an available outcome, or another defined group. The record also does not describe interim analyses, stopping rules, or whether the outcomes were analyzed according to a prespecified protocol. These omissions do not invalidate the displayed summaries, but they limit assessment of how completely they reflect the trial’s planned analysis and how robust they are to missing data or multiple testing.
11. Safety Results
The registry reports serious adverse events as affected participants divided by participants at risk.
| Arm | Participants with serious adverse events | Participants at risk | Percentage |
|---|---|---|---|
| Insulin | 16 | 490 | 3.3% |
| Usual Care | 5 | 490 | 1.0% |
Other (non-serious) adverse events
Participants with at least one non-serious event at or above the registry's 1% reporting threshold.
| Arm | Participants affected of at risk |
|---|---|
| Insulin | 15 of 490 |
| Usual Care | 19 of 490 |
Most frequent serious adverse event terms
| Event term | Organ system | Insulin | Usual Care |
|---|---|---|---|
| Severe hypoglycemia (BG < 40 mg/dL) | Endocrine disorders | 16 of 490 | 5 of 490 |
Most frequent non-serious adverse event terms
| Event term | Organ system | Insulin | Usual Care |
|---|---|---|---|
| Hypokalemia (K < 2.0 mmol/L) | Endocrine disorders | 15 of 490 | 19 of 490 |
Serious events with the highest arm-level rate: severe hypoglycemia (bg < 40 mg/dl) (3.3%).
The registry reports adverse-event counts for groups of 490 participants in each arm. In the Insulin group, 16 participants are recorded with serious adverse events and 15 with other adverse events. In the Usual Care group, 5 participants are recorded with serious adverse events and 19 with other adverse events. The registry’s adverse-event summary does not provide confidence intervals or a comparative statistical analysis for these counts. They are descriptive counts and should not be converted into a causal conclusion by themselves.
The most frequently listed serious adverse-event term is Severe hypoglycemia (BG < 40 mg/dL), reported as 3.3%. The record does not provide a group-specific count for this term in the information posted, so its distribution between the two arms cannot be determined from this summary. The registry also does not provide further detail about event timing, severity grading beyond the serious classification, or how events were attributed.
Serious and other adverse events are distinct categories in the registry summary. The counts do not necessarily represent the number of unique event episodes, and the record does not state whether a participant could contribute to more than one category. They should therefore be read as the registry reports them, without adding assumptions about overlap or calculating rates. The information is useful for describing what was recorded, but it is not a complete comparative safety analysis.
12. What the Result Does, and Does Not, Mean
The registry results establish a descriptive record of the trial’s two strategies and their posted outcomes. For the primary endpoint, the tight-control arm has a lower recorded infection rate than the standard-care arm. Because no confidence interval or inferential comparison is posted for that count-based endpoint, the statistical precision of the apparent difference is not available. The displayed values alone cannot show whether the underlying rates differ or how large any underlying difference might be.
The secondary comparisons are also limited in what they establish. Their intervals include the no-difference value, and they are reported without adjustment for multiple comparisons. That does not prove that the strategies have identical effects on mortality or cognitive scores. Rather, the posted results do not precisely distinguish a difference from no difference, and the registry does not provide the analysis-plan details needed for a fuller confirmatory interpretation.
These results do not establish that tight glycemic control improves recovery overall, nor do they show that it fails to do so. The primary endpoint measures a specific infection rate during the cardiac ICU stay. Other outcomes concern different events and time frames. A single endpoint cannot stand in for every aspect of recovery, and unreported secondary results cannot be inferred from the outcomes’ names in the registry.
Likewise, the adverse-event counts are descriptive and lack a reported comparative analysis. The severe hypoglycemia term is listed, but the posted summary does not specify its distribution by arm. The data should not be used to infer an individual participant’s risk or to make treatment decisions.
In general, the strength of a statistical conclusion depends on the design, the completeness of outcome data, the analysis methods, and the precision of estimates as well as their point values. Several of those details are not reported in the registry record. The most defensible reading is therefore narrow: describe the recorded group results, recognize uncertainty in the comparisons, and avoid treating unadjusted or unavailable analyses as definitive evidence.
13. Why This Trial Matters Statistically
The trial is statistically informative because it illustrates the difference between a primary outcome value and a complete estimate of a treatment contrast. The registry reports infection rates for both randomized groups, but not a confidence interval or test for the primary count outcome. A reader can identify the observed ordering, yet cannot judge its precision from the posted primary results. This is a useful reminder that reporting group summaries alone may not answer the comparative question.
It also highlights the importance of matching analysis methods to outcome type. Infections per patient time are a rate, mortality is binary, and cognitive scores are continuous. Those measures require different summaries and can have different sources of uncertainty. A result on one scale cannot automatically be combined with another to create a single overall conclusion.
The posted secondary comparisons demonstrate why point estimates, intervals, and multiplicity context should be read together. A point estimate can appear small or large without indicating how precisely it is known. Confidence intervals communicate uncertainty, while unadjusted p-values do not account for the full set of outcomes under consideration. The registry does not describe a multiplicity plan, so secondary findings deserve cautious interpretation.
Finally, planning illustrations based on observed effects should not be mistaken for the original design or for observed power. They answer hypothetical questions under stated assumptions. Keeping that distinction clear helps prevent post hoc calculations from being treated as evidence about trial adequacy or clinical importance.
14. 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 principal limitation for interpreting the primary result is that the registry posts the two group infection rates but not a comparative estimate, confidence interval, p-value, or described model. Without those, the precision of the primary comparison cannot be assessed. The registry marks the two-arm comparison as missing or not estimable for this count outcome. The rate’s stated unit and ICU observation period are available, but details of the primary analysis are not.
The record does not report the sample-size justification or the statistical analysis plan. It therefore does not establish the effect size the trial was designed to detect, the assumptions used for its original design, or whether the posted summaries follow a prespecified method. The planning illustrations are explicitly based on observed effects and should not be used to reconstruct the original rationale.
The trial was unmasked according to the registry. For outcomes involving clinical judgment or classification, knowledge of treatment assignment can be relevant to how care is delivered or outcomes are assessed. The registry describes the infection criteria as CDC-defined but does not provide enough detail to evaluate adjudication procedures or the potential influence of unmasked assessment.
Outcome denominators vary, and missing-data handling and analysis populations are not reported. The record does not explain why fewer participants contribute to some secondary outcomes than to the primary endpoint, or whether sensitivity analyses were performed. The number of secondary outcomes and absence of a reported multiplicity strategy also make isolated unadjusted results less secure as confirmatory findings.
Finally, the registry record does not provide inferential results for several listed secondary outcomes. Their inclusion in the outcomes list cannot fill that gap. These limitations concern the information available in the registry record and should not be interpreted as proof that analyses were not conducted elsewhere.
15. Related Tutorials
16. Related Statistical Calculators
17. Sources
- ClinicalTrials.gov: SPECS: Safe Pediatric Euglycemia in Cardiac Surgery — NCT00443599.
- Registry record last updated 2022-07-25; status last verified 2022-07.
- Results first posted 2014-03-10.
- 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.
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18. Record Summary
SPECS (NCT00443599), sponsored by Boston Children's Hospital, is recorded as a completed randomized, parallel-group trial with no masking and an enrollment of 989. The study compared insulin infusion targeting blood glucose of 80-110 mg/dL with standard care in which insulin use was at the treating clinical team’s discretion.
The primary endpoint was cardiac ICU nosocomial infections per 1000 patient days. Posted rates were 8.6 for Tight Glycemic Control and 9.9 for Standard Care, with 490 participants reported in each arm. No inferential primary comparison is posted. Secondary results include mortality at hospital discharge, mortality at 30 days, and cognitive scores at one year; their unadjusted comparisons are imprecise, and no sponsor-reported analyses are listed.
The registry does not report the statistical analysis plan, missing-data methods, analysis populations, or multiplicity strategy. The recorded results support descriptive interpretation, while conclusions about the precision and robustness of the primary comparison remain limited by the information available in the registry record.