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To the Editor.—
I read with interest the article you have published on the outcome of neonates cared for in different size units.1 As a provider of care who has worked at both community-based and regional medical centers, I have several questions and points of discussion.
The highest mortality rate is found in neonates weighing <2 kg delivered at hospitals without neonatal intensive care unit (NICU) care (159 sites). I think few would argue that no infant should be delivered at a hospital without a neonatal resuscitation team. How many of these "no NICU units" have regular neonatal resuscitation programs (NRPs)? The median number of neonates with a birth weight <2 kg delivered at the "no NICU sites" was 4.5 per year. However, it is also clear that at least 1 unit had 31 such deliveries per year. What are the maternal demographics of mothers delivering at these sites? Do they have access to (do they receive) prenatal care? Have the authors visited this unit to determine if the problem identified in 1992 and 1993 still exists in 2002?
Clinical recommendations have been made based on statistically insignificant results. It is one thing to report these results; it is another to make policy decisions that are not supported by the evidence presented. If 1.29 (95% confidence interval [CI]: 0.74–2.25) presented in Table 3 for neonates (birth weight [BW]: 1250–1999 g) cared for in intermediate NICUs is considered clinically important, then the finding that "major teaching hospitals" did worse must also be considered clinically important (odds ratio [OR]: 1.39; 95% CI: 1.04–1.86). If we are to use nonstatistically important differences, I could use the data in Table 2 to suggest that neonates should be born in for-profit hospitals (0.82 CI: 0.65–1.03). This finding is closer to being significant than any of the data in the >1250 g groups. How do the authors explain these findings, and why are they not discussed in the article?
If the authors argue that there is a missing factor not included in the model that accounts for the poor performance of major teaching centers and not-for-profit hospitals, the model is flawed. In fact, I believe this is the case. Two other findings make this likely. First, being small-for-gestational age (SGA) does not confer a survival advantage. When maturity and birth weight are considered, both the degree of immaturity and size of the infant influence survival. In a recent look at neonates admitted for NICU care, neonates classified as SGA had higher mortality rates at every gestational age.2 Second, I know of no studies that suggest that respiratory distress syndrome confers a survival advantage. In fact, one of the leading causes of infant death for 1999 was respiratory distress of the newborn.3 Can the authors offer us some insights as to how they explain their findings? Is it possible that respiratory distress was entered into the model as inverse (ie, as 0 instead of 1)?
Did the authors try to look at neonatal groups that provided care at both types of units? Many large (university-based and private practice) groups provide care at both types of units in their area. At both Duke and Emory universities, I personally provided care at NICUs with <15 beds (Durham Regional and Floyd Medical Centers, respectively). Did the authors look to see if the level of training/experience of the individual who provided the care influenced outcomes?
Finally, the assertion "that mortality has not declined markedly in the intervening years" is not supported by recent reports. Recent papers show a continued improvement in infant mortality rate and, in part, attribute this improvement to advancements in neonatal services.4–8 Dr Carlo is co-author on an article which states that in the early 1990s, "Survival for infants between 501 and 1500 g at birth continued to improve, particularly for infants weighing <1000 g at birth. This improvement in survival was not associated with an increase in major morbidities, because the incidence of chronic lung disease (CLD), proven necrotizing enterocolitis (NEC), and severe intracranial hemorrhage (ICH) did not change."9 In addition, the units providing neonatal service have changed. Can the authors provide statistics to show that the number of neonates cared for at different levels of care have remained static? It is hard to believe that 1992 data on neonatal units is applicable in 2002.
I look forward to the responses from these highly respected and well-published authors.
REFERENCES
Janet Bronstein, PhD
School of Public Health
University of Alabama at Birmingham
Birmingham, AL
Ciaran S. Phibbs, PhD
Susan K. Schmitt, MS
Health Economics Resource Center
Center for Health Care Evaluation and Cooperative Studies Program
Veterans Affairs Palo Alto Health Care System
Palo Alto, CA
Department of Health Research and Policy
Stanford University, Stanford, CA
Roderic H. Phibbs, MD
Department of Pediatrics and Cardiovascular Research Institute
University of California
San Francisco, CA
Waldemar A. Carlo, MD
Department of Pediatrics
University of Alabama at Birmingham
Birmingham, AL
Dr Clark’s comments seem to indicate some misconceptions about the nature of the data we used in this study and about the types of conclusions that can be drawn from our findings. Our analysis looked at risk-adjusted mortality of infants born at hospitals with different levels of NICU care. The outcome is the product of the total system of care (ie, obstetrics and newborn care), including all of the health care professionals involved in those services. We found that a higher NICU census and level of care identified those hospitals with, on average, better performance of that system of care. This is an association, not cause and effect. There are several rather obvious hypotheses that could be put forward to explain this association, but testing these would require different data. Of note, because several of Dr Clark’s comments and questions refer to neonatologists, is that it is our belief that many of the most important differences across types of hospitals may be related to how systems of care are organized and to other health care professionals.
The relation between a high volume of cases and better outcomes has been demonstrated in many areas of health care representing a wide spectrum of conditions, mortality risk, and complexity of care, including cardiac surgery, mammography, prostate surgery, trauma care, and pediatric intensive care.1–6 As we noted with multiple references in our article, many previous studies have found volume-outcome and/or level of care relationships for all births, and for selected high-risk subsets of births. Our study looked at how these relationships held up over various segments of the low birth weight spectrum. Given all of the previous evidence, it should be no surprise that we found large volume-outcome and level-of-care relationships over the entire low-weight spectrum. Mortality is lower when high-risk births occur in hospitals with large tertiary NICUs. In fact, there is new evidence that the volume relationship extends to low-risk deliveries.7,8
We used data on births in all of California (over 10% of the nation). The advantage of this very large data set is that uncommon outcomes such as neonatal death can be analyzed. The disadvantage is that such data sets do not contain the detailed information needed to answer some of Dr Clark’s questions such as the level of training for the pediatric staff or the quality of the NRPs at individual hospitals. With respect to his concerns about the births occurring in level I (no NICU) hospitals, many, but not all, were located in rural or semirural areas. Thus, there are geographic constraints on the movement of high-risk mothers to tertiary centers for delivery, which will result in some increase in the rate of delivery of very small infants.
Dr Clark is incorrect about our drawing conclusions from statistically insignificant results; our clinical recommendations were based on statistically significant results. The specific result he cites is from a model that looked at a subset of larger infants and thus relatively few deaths, which drives the statistical power of the analyses. We specifically noted in our discussion the limitations of our statistical power and how we made inferences from these data. The odds ratios for all of the levels of care and birth weight intervals presented in Table 3 are >1, most of them are much larger, and most are statistically significant. The results that are not statistically significant are either: 1) for larger infants born in smaller units, which combine to yield little statistical power, or 2) for infants born in hospitals with large community NICUs where the odds ratios (OR) are relatively close to 1.0. Taken together, these data provide strong evidence that mortality for infants with BW <2000 g is lower when they are born at hospitals with large regional NICUs.
With respect to Dr Clark’s comments about some of the seemingly strange coefficients in the risk model, one has to remember that these results represent correlation, not causation. In response to his comments, we re-estimated the models deleting the variables he mentions (ownership, teaching status, SGA, and respiratory distress syndrome [RDS]) and our results are robust to dropping these variables. The protective effect in the model of RDS surprised us at first. In unreported results, we estimated a model that let the RDS estimate vary by each BW group. For infants with a BW <750 g, the odds ratio (OR) was 0.16. The OR was between 0.5 and 0.6 for infants in the 750- to 999-g and 1000- to 1249-g BW groups, and about 1.05 for larger infants. Although it would need chart reviews to confirm this, we are almost certain that this is a data coding issue. Most of the infants who die with a BW <1000 g do so very quickly; in our data over 75% of those with a BW <750 g, and over 50% of those with a BW between 750 g and 999 g, died on the day of admission. Many of these infants will die before a formal diagnosis of RDS can be made, which would cause the observed statistical results.
The decades-long decline in low birth weight neonatal mortality has ended for the time being. An article from the Vermont-Oxford Network shows that mortality declined from 1991–1995 and has not changed since then.9 This pattern is also reflected in several of the references cited by Dr Clark. The net effect is that although data are fairly old (1992–1993), the aggregate change in mortality rates between our data and current rates is quite small. Further, there is nothing in the time trends that we know of that would lead us to look for differences in the relative mortality rates across levels of care.
REFERENCES
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