THERAPY

Criteria abstracted from The Users' Guides to the Medical Literature series in JAMA

Pediatr Crit Care Med. 2009 10(4):460-466.[abstract]

Review posted June 29, 2010

1. What is being studied?

   The study objective:

   To test the safety and efficacy of an enteral feeding algorithm in infants with HLHS following stage I palliation.

   The study design:

   Single-center, prospective case series with historical comparisons.
   
   The patients included:

   Consecutive patients >35weeks gestational age and weight >2kg admitted in the cardiac intensive care unit over an 18-month period following stage I palliation of HLHS (n=36).  These patients were compared with a similar cohort of patients admitted to the CICU over an 18-month period before the implementation of the feeding algorithm (n=27).         
   
   The patients excluded:

   Nonsurvivors, patients on ECMO prior to feeding initiation, those with a history of NEC or fetal intervention.

   The interventions compared:

   A feeding algorithm was implemented in the study group in the postoperative period for initiation and advancement of enteral nutrition.

   The outcomes evaluated:

   Median duration of TPN; Median time to achieve recommended daily allowance of calories defined as 108Kcal/Kg per day; Incidence of NEC; Time to first feeding; growth measurements; length of intubation; length of stay in the CICU and hospital.

2. Are the results of the study valid?

   Primary questions:

   1. Was the assignment of patients to treatments randomized?

      No. There was a prospective  data collection for the study group and retrospective chart review for the control 
      Group.

   2. Were all patients who entered the trial properly accounted for and attributed at its conclusion?

      Was follow-up complete?

      All of the patients from the study group used the algorithm and were followed throughout the study to assess the safety of the algorithm. There were 18 infants who converted to breastfeeding and 11 who were discharged before reaching the feeding goal. Data from these infants was included only to the point of breastfeeding initiation or discharge.

      Were patients analyzed in the groups to which they were randomized?

      They were not randomized, but obviously the two groups were distinct in time so there was no cross over between groups. There is no mention of patients in the study group who did not stay on the protocol and would then essentially be control patients.

   Secondary questions:

   3. Were patients, health workers, and study personnel "blind" to treatment?

      There was not need to blind the personnel because there was only one prospective group.

   4. Were the groups similar at the start of the trial?

      There was similar gestational age, Apgar scores, weight, PRISM score at 24 hrs postop, gender distribution, diagnostic groups. However there was a change in surgical practice that occurred during the study.

   5. Aside from the experimental intervention, were the groups treated equally?

      No. Some of the patients of the study group had a different procedure done. All patients in the control group underwent a Norwood-BT Shunt (NBTS) whereas only 33% of the study group underwent NBTS; the remainder received a Norwood with an RV-PA conduit (Sano). Given the altered hemodynamics following this procedure, this could be a significant confounding variable.

3. What were the results?
   
   
   1. How large was the treatment effect?

      The study group had shorter duration of TPN (51 vs. 116 hrs. p=0.03). The median time to achieve recommended daily allowance (RDA) of calories was significantly reduced in the study group (9 vs. 13 days. p=0.01). There were no cases of NEC on the study group vs. 3 cases on the control group, though this difference was not statistically significant (p=0.07).

   2. How precise was the estimate of the treatment effect?

      The study does not provide  data on precision of the significant differences – duration of TPN use and time to achieve RDA – for determination of precision of these results. A p value alone does not provide any estimate of precision; they could have reported interquartile ranges of time or 95% confidence intervals.

      In calculating the difference in the incidence of NEC, we see an absolute risk reduction of 0.11, but with 95% CI from -0.017 to 0.24. So the true incidence of NEC in the study group could be anywhere from 1.5% higher than the controls, or 24% lower. A simple rule of thumb to use when the rate of events is zero to calculate the upper 95% CI is to calculate 3/n (1). In this case, 3/36 is roughly 10% - the possible rate of NEC in the study group.

4. Will the results help me in caring for my patients?
   
   
   1. Can the results be applied to my patient care?

      I think they can be applied but still I would like to see more studies comparing HLHS patients that have BT-Shunt vs Sano done and see if there is any difference between them.

   2. Were all clinically important outcomes considered?

      I think some of the most important outcomes for this specific patient population were considered by this study though this study excluded nonsurvivors. We want to know if there was a difference in mortality between the two groups.

   3. Are the likely treatment benefits worth the potential harms and costs?

      Presumably saving a few days of TPN would save money. We cannot conclude anything about harms, since at least with regard to NEC, we cannot rule out an increased risk in the study group.

References:

1. Hanley JA, Lippman-Hand A. If nothing goes wrong, is everything all right? JAMA 1983; 249: 1743-1745.

Last Updated: June 29, 2010

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