Running for Neonates, and their families

On April the 23rd I will be running a half marathon, as part of the PAF-Néonat team of Sainte Justine Hospital.

We are raising funds for the partnering with families program, which involves parents in clinical care, research and education in our neonatal service.

We have a quite innovative program and want to expand it further.

Our team for the run includes children, parents, and professionals, who will be running anything from 0.5k (children only!), 5k, 10k or the 21 kilometer half marathon.

To make a donation click on this link neonat-paf.ca, at least 95% of the funds raised go directly to support our program.

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Reading Research: Subgroups and Observational studies

In publications of randomized controlled trials, subgroup analyses are frequently performed. The idea behind such analyses being to determine whether one group or another has a different result to the overall results, for example, whether boys or girls have more benefit from an intervention. Sometimes this is done to try to salvage some possibly positive results when the overall result is negative, sometimes to try to refine indications for interventions based on the results.

The first thing to realize is that it would be bizarre if every subgroup had exactly the same result from an intervention, just based on random effects. Simply because, to use my own example, girls had more improvement in a particular outcome than boys, does not mean that the difference is due to some biologic difference between them, it may just be chance, and the next trial might show more impact in boys than in girls.

Interpretation of subgroup analyses always has to be taken with a grain (or even a handful) of salt.

When you examine the results of your trial and then decide to do a subgroup analysis based on a suspicion that the girls did better, you are entering dangerous territory. Such post-hoc subgroup analyses should be avoided like a plague, it is far too easy to be led astray; if by chance blond babies did much better with the intervention and brunettes only did slightly better, and you notice in your data set that this is the case, and then do statistical analysis to show that the results are significant in blonds, and not in brunettes, what should you do? The best idea is to not do such analyses. Stick with subgroup analyses that were decided before the study was started based on a reasonable supposition that one group or another might have a different response. Deciding a priori on a small number of subgroups that might feasibly have different responses, (and not a priori listing every subgroup that you can think of) is the first step. Then the statistical analysis requires an evaluation of the interaction between the intervention and the subgroup, it is not enough to show a significant result in one group and not in another, it requires a statistical test to show that the responses are actually different, and that such a difference is unlikely to be due to chance.

Even when you do all that, the only way to be sure that the difference is real, is to do a prospective trial, which might only include the group who had the apparent benefit, if the overall study was a null trial. Post hoc subgroup analyses are not usually strong enough evidence to even do that, which is why a clear statement of whether a subgroup analysis was decided before or after commencing the trial is important, and why publication of protocols, including a description of planned subgroup analyses, is important.

Sometimes things change during a trial, I remember a trial of an established medication, and the company changed the preparation part way through the trial, which changed bio-availability dramatically, which mandated a subgroup analysis that was not planned before starting. Of course in such a circumstance the publication should describe exactly what was done and why, and why the subgroup analysis became important. Something similar happened in the oxygen targeting trials, when Masimo recalibrated the oximeters in use in several of the trials, the changes in saturations actually achieved required a subgroup analysis.

A publication from 2012 investigated claims of significant subgroup effects in RCTs, and showed that only 50% reported a significant test of interaction (and only 2/3 of those actually reported the test or gave the data). Sun X, et al. Credibility of claims of subgroup effects in randomised controlled trials: systematic review. BMJ. 2012;344:e1553.
That study included a list of criteria for deciding whether a claim of a subgroup effect might be reliable:

Ten criteria used to assess credibility of subgroup effect

Design
  • Was the subgroup variable a baseline characteristic?

  • Was the subgroup variable a stratification factor at randomisation?*

  • Was the subgroup hypothesis specified a priori?

  • Was the subgroup analysis one of a small number of subgroup hypotheses tested (≤5)?

Analysis
  • Was the test of interaction significant (interaction P<0.05)?

  • Was the significant interaction effect independent, if there were multiple significant interactions?

Context

  • Was the direction of subgroup effect correctly prespecified?

  • Was the subgroup effect consistent with evidence from previous related studies?

  • Was the subgroup effect consistent across related outcomes?

  • Was there any indirect evidence to support the apparent subgroup effect—for example, biological rationale, laboratory tests, animal studies?

A new publication in JAMA Internal Medicine (Wallach JD, et al. Evaluation of Evidence of Statistical Support and Corroboration of Subgroup Claims in Randomized Clinical Trials. JAMA internal medicine. 2017) specifically looked at subgroup analyses in published RCTs. The investigators examined whether such analyses were performed, whether appropriate statistical tests of interaction were performed, how common significant differences were, and then whether any follow-up studies had been done. They found 64 RCTs with 117 analyses making claims of important subgroup differences and :

Of these 117 claims, only 46 (39.3%) in 33 articles had evidence of statistically significant heterogeneity from a test for interaction. In addition, out of these 46 subgroup findings, only 16 (34.8%) ensured balance between randomization groups within the subgroups (eg, through stratified randomization), 13 (28.3%) entailed a prespecified subgroup analysis, and 1 (2.2%) was adjusted for multiple testing. Only 5 (10.9%) of the 46 subgroup findings had at least 1 subsequent pure corroboration attempt by a meta-analysis or an RCT. In all 5 cases, the corroboration attempts found no evidence of a statistically significant subgroup effect.

Most claims of a subgroup difference, then, are not supported, even by the evidence in the actual publications where the claims are made (note to anyone involved in peer review, make sure that statistical tests of interaction are reported before accepting that subgroup differences might be real). In the few cases where later randomized trials are performed which tried to determine whether there really were subgroup differences, they were all negative.

In neonatology, one study which answered most of the above criteria is from the CAP trial: Davis PG, et al. Caffeine for Apnea of Prematurity Trial: Benefits May Vary in Subgroups. The Journal of pediatrics. 2010;156(3):382-7.e3. That secondary analysis showed that age at starting treatment (a baseline characteristic, but not a prespecified subgroup, or a factor for stratification) had a significant impact on the age of  extubation and the age of stopping oxygen. Starting treatment before 3 days had a greater impact than after 3 days, and the interaction was significant, at least for postmenstrual age at last extubation and post-menstrual age of finally stopping CPAP. That publication also showed that the infants who were receiving positive pressure ventilatory support at randomization also had a greater impact on their neurodevelopmental outcome. Both of these findings are biologically plausible, and both are accompanied by subgroup differences for other outcomes which (even if not statistically significantly interactions) were in the same direction, such as a reduction in bronchopulmonary dysplasia.

Observational studies also need to be carefully interpreted. Methods for adjusting for baseline risk differences in cohort studies, such as multivariate regression, propensity analysis and instrumental variable analysis, might help to balance groups for prognostic variables, but there will always remain the potential for unknown prognostic variables to bias the results. A fantastic new addition to the “Users’ guides to the medical literature” series in JAMA has just been published.   Agoritsas T, et al. Adjusted analyses in studies addressing therapy and harm: Users’ guides to the medical literature. JAMA. 2017;317(7):748-59.  A great read for anyone who uses the medical literature and sometimes reads observational studies, which I think is most of us. They describe the various methods of adjustment (in non-statistican language, thankfully) including the “instrumental variable analysis” which was new to me as a term, but the concept is simple. When variations in the application of a treatment occur which are not related to prognosis, then you can use that variation as a substitute for randomization. In other words if a treatment is applied differently in one hospital compared to another (such as inhaled NO in the very preterm) but the hospitals treat the same kind of patients, with the same risk characteristics, then you can use that fact to mimic cluster randomized allocation. The problem is that even the statisticians can’t agree exactly how to do that, and there is still a possibility of unbalance in other prognostic factors.

The authors of the article end with a list of major publications that reported observational studies showing a positive or negative effect of a medication, which was disproved by prospective randomized trials

Comparative effectiveness research relying on observational studies using conventional or novel adjustment procedures risks providing the misleading effect estimates seen with hormone replacement for cardiovascular risk, β-blockers for mortality in noncardiac surgery, antioxidant supplements for healthy people, and statins for cancer. If RCTs cannot be conducted, it will remain impossible to determine whether adjusted estimates are accurate or misleading

The abstract ends with this sentence “Although all these approaches can reduce the risk of bias in observational studies, none replace the balance of both known and unknown prognostic factors offered by randomization.”

 

 

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Survival of extremely preterm babies, part 3. A regional European comparison. If you don’t treat them, they will die.

Hard on the heels of the publication discussed in the previous post, a new publication comparing interventions and outcomes for babies at the same sort of gestational ages from 12 regions in 5 different European countries (if we can still call the UK European!)

You have to do some of your own arithmetic to find out what is going on here, the denominator for all the presented data is the total number of births, which includes stillbirths, and babies not receiving active care. For example, at 22 weeks and less than 500 g, there were 3 babies in the Italian regional cohort (of 34 births) that received respiratory support, which is 9%, but there were only 6 live births in this category, which mean that 50% of live births received such an intervention, in none of the other regions did any such babies (under 500g and 22 weeks gestation) receive respiratory support.

Over 500g there were 4 babies in Italy, and 1 in Portugal that received respiratory support, and no survivors in any of the regions.

I really don’t see the point of reporting survival and the other data among all births, when many were stillborn, but not presenting survival among live births or among those who received active care. It is not surprising for example that the Portuguese region did not provide respiratory support for any of the 22 weekers of less than 500g because they were all stillborn!

The authors suggest that this was to “improve comparability between countries where there are differences in whether a birth is reported as live or not” which implies that they did not have a common definition of a live birth between the regions, and means that the data become much less useful. It is also in contrast to an earlier statement in the methods “the use of the common EPICE recruitment criteria allowed to overcome these differences and provide comparable data across the five countries”.

Here is one figure from the publication:

graphic-1-large

You can see at 23 weeks gestation that the only survivors are in Italy and the UK. Under 500g there was one baby in the UK that had respiratory support, who died, and 3 in Italy with one survivor. You can calculate therefore that survival at 23 weeks and under 500 grams is actually 25% if you institute active intensive care! Not bad… but that percentage would be almost as meaningless as the number in the table 3 which calculates a survival of 1%, among all the 88 births in that weight and gestation category, live births, still births and babies not receiving respiratory support included.

At 23 weeks and over 500 grams there were no babies receiving intensive care in the French regions, 1 in the Belgian region, 1 in the Portuguese region, 24 in the Italian cohort and 30 in the UK. The only survivors were in Italy and the UK with 7 and 14 survivors respectively.

The conclusion in the abstract of this study ends like this:

Universally poor outcomes for babies at 22 weeks and for those weighing under 500 g suggest little impact of intervention and support the inclusion of birth weight along with gestational age in ethical decision-making guidelines.

Er, No. “Universally poor outcomes for babies at 22 weeks and for those weighing under 500g who did not receive intervention suggests that if you don’t actively treat babies in the periviable period, they all die.”

I do think there is useful and interesting information in this publication, but I think you should take the statistical significance of some of the testa with a grain of salt, the 2 babies treated in the Italian region under 500g at 22 weeks is “significantly” different to the zero treated everywhere else, but does it mean anything?

I think the authors are right that birth weight is as important as gestational age in decision making and should be taken into account when estimating survival, and counselling parents. Birth weight is only known with accuracy after birth, however, and I don’t think that these data give a real justification for using a universal cutoff of 500 grams, chosen arbitrarily for this article. Why not 550 grams? or 454? I think it is unlikely that there is any step-wise sudden improvement in survival between 499 grams and 501 grams, just like gestational age, which doesn’t come in distinct 7 day bundles, and is never known with certainty (except after IVF), we should nuance our counselling, with the real uncertainties in our data and the gradual improvements in survival with increasing hours and days of gestational age and increasing grams of birth weight.

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Survival of extremely preterm babies in a national cohort, and a comparison of nations.

As a follow up to my last post, a new article from Norway details the survival to one year of age, and the neonatal morbidities of babies born at 22 to 26 weeks gestation in the whole country in 2013-2014. (Stensvold HJ, et al. Neonatal Morbidity and 1-Year Survival of Extremely Preterm Infants. Pediatrics. 2017).

A great thing about this article is that the numbers of fetuses/babies alive at each point are detailed in the first table, of the 420 babies delivered. 335 were alive when the mother was admitted to hospital, 145 were stillborn, leaving 275 who were liveborn, and 251 admitted to a neonatal unit.

As you can see from the data below, more babies are stillborn at 22 and 23 weeks than later, after being alive on admission to obstetrics; probably a major part of that difference is an unwillingness to actively intervene, especially to perform cesarean deliveries, when the expected mortality is very high.

norway-survival

What is quite obvious is that survival is very different depending on which denominator is used, these data are a very clear example of that; changing from 5% among all births to 60% among those admitted to NICU at 22 weeks gestation (60% being 3 of the 5 babies actively treated).

norway-survival-2

Another nice feature of this article is that the modes of death are reported: of the 66 deaths there were 34 that followed a decision to redirect care. The authors don’t report these data by gestational age, but I wouldn’t be surprised if redirection of care occurred more rapidly in the most immature babies. Seventeen of the 34 redirections of care occurred because of severe intracranial hemorrhage, which, given the poor predictive value of head ultrasound, is a practice we should re-consider.

The authors then compare their data to recent European publications of national cohorts of extremely preterm infants. As you can see the percentage of babies admitted to intensive care was similar in Norway and Sweden, lower in the UK at 22 and 23 weeks, and a little lower at 24 weeks, and very different in France, with almost no admissions at 22 or 23 weeks, and many fewer at 24 weeks gestation. As for survival, despite a similar proportion receiving intensive care, babies in Sweden were more likely to survive at 23 and 24 weeks, than the Norwegian babies. In the UK the survival was almost non-existent at 22 weeks and much lower at 23 weeks, and the French babies never survive before 24 weeks, and even at 24 and 25 weeks survival is lower.

image1

Finally the authors of this study compare their outcomes to a previous national cohort from 1999-2000, and suggest that, although the proportions dying before obstetric unit admission increased, and the NICU admissions increased overall, (putting together the 22, 23 and 24 week gestation babies) there was no increase in overall survival. But in the first cohort there were only 2% of babies born at 22 weeks admitted to the NICU (1 baby) and 23% of live births at 23 weeks. With the change in the distribution of gestational age among babies admitted to the NICU, and many more of the most immature babies being actively treated, the fact that the survival among live born infants did not change (44% to 41%)  and the survival among infants admitted to NICU was also unchanged (44/83, 53% compared to 50/99, 51%) is to my mind a trend in a positive direction.

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Improved survival and improved Bayley scores among infants born in the periviable period.

If you were to report survival and other outcomes among infants with a very high risk of dying or having long-term impairments, why would you include babies for whom a decision was made to let them die?

Let me put it this way, if 1000 babies are born in each of 2 epochs, and 900 are left to die, and the survival rate was 40% in the first epoch, and 60% in the second, among the 100 babies who were treated, then this is either not significantly different p=0.051 or highly statistically significant p=0.0072, depending on whether you analyze the data using the denominator as all live births, or only the live births who received active care with an attempt to have them survive.

In a brand-new report in the FPNEJM, almost all of the data regarding survival and long-term outcomes are presented as proportions of live births. The denominator used for almost all of the analyses was the 4274 live births, of whom over 1000 did not receive active care, leaving 3158 for whom neonatal intensive care was instituted.

I can see reasons for doing some of the analyses like this: if the decision not to intervene was made based on an analysis of risks, and only the very highest risk babies were not actively treated, then leaving them out could skew the data, and make them look more positive. But in reality we know that the major determinant of whether you get intensive care in this gestational time period (in the NICHD NRN, and I am sure in many other places also) is the hospital that you are born in, not their risk profile necessarily.

However, in those hospitals that are selective in treating the most immature babies, if the babies who were not treated did indeed have a higher risk of mortality, then leaving them out would make the data look better than they would be if all infants received active treatment.

That is indeed what the previous NRN data seem to show. In the paper from 2015, examining data from 2006 to 2011, it was the centers that treated all the babies who had the best survival when expressed as a proportion of live births, ranging from 10 to 20% at 22 weeks, for example. But if you look at survival among all those who received active treatment (including the babies from the universal treatment hospitals) at 22 weeks 23% survived, which is a little better than the survival in the centers that treated all the babies. Those hospitals that treated none of the 23 week infants had no survivors.

So how should we calculate survival rates? If there are many babies not receiving active treatment, then a shift to treating more babies might decrease the proportion of survivors among those treated, but increase the total survival among the  live born.

I think that both numbers should be reported, as well as the numbers not actively treated, that is the only way you can really understand what is happening.

The new publication from the FPNEJM (Younge N, et al. Survival and Neurodevelopmental Outcomes among Periviable Infants. The Formerly Prestigious New England journal of medicine. 2017;376(7):617-28.) concentrates on survival among all live births of less than 25 weeks gestation, and barely reports survival and outcomes among those infants who received active care: only the Odds Ratios for those outcomes being reported in one section at the end of table 4.

It is possible to calculate some of the other outcomes, with the proviso that the exact numbers could be slightly different  to the numbers I present below, depending on rounding errors, and other sources of variation.

The article reports outcomes from 3 non-overlapping epochs, infants born in 2000-2003, 2004-2007, and 2008 to 2011. They include data from 11 centers that were part of the Neonatal Research Network (the NRN) in all of those years. The previous study I mentioned had data from 25 centers that were members of the NRN from 2006 to 2011, so these new data include a subset of the data from Rysavy MA, et al. (Between-Hospital Variation in Treatment and Outcomes in Extremely Preterm Infants. The New England journal of medicine. 2015;372:1801-11) and add to that data from earlier years, and give more information about outcomes at about 2 years, the Bayley scores from version 2 for the earlier epoch, changing to Bayley 3 during the second Epoch. They use different thresholds for developmental delay for the different versions of the BSID, and concentrate on the cognitive composite from version 3.

The data show an improvement in survival (a small improvement but not likely to be due to chance) and an improvement in survival without the famous NDI (which, from here on, I will call neurological impairment or developmental delay, NDDI. I continue to insist on the fact that a low Bayley score is NOT an impairment, but a screening test showing a potential delay in development). For example at 23 weeks the frequency of that outcome increased from 7% to 11% to 13%, when calculated based on all live births, but increased from 9% to 16% to 19% when calculated based on babies who received active treatment.

Overall survival at 23 weeks is reported as 20%, 20% and 24% in the 3 epochs as reported in the article, but, when based only on those who received active treatment, it is 27%, 28% and 35%.

I have seen comments that these data show absolutely no improvement at 22 weeks, but in fact, expressed as survival among those who received active treatment, survival increased from 10% to 21 % and 17%, which may not be statistically significant, but is about a doubling of survival from the first epoch to the 2 later epochs.

Survival does seem therefore to be improving, the proportion receiving active treatment has not changed, however; in this study the improvement in survival is therefore probably a real improvement in our capacity to look after these babies, rather than a change in who we select for intensive care.

Among survivors, the proportion with NDDI has decreased somewhat, the discussion of the article puts it like this

the rate of survival without neurodevelopmental impairment and the rate of survival with neurodevelopmental impairment increased similarly (adjusted relative risk, 1.27; 95% CI, 0.99 to 1.65).

I guess ‘increased similarly’ is the way that is stated because the lower 95% CI is 0.99, I think you could put that differently and state that, among survivors, the Odds of not having NDDI increased from the 1st to the 3rd epoch, by a factor of 1.27. Although the CI include 1.0, I think that is very reassuring.

With this improvement in survival, I think there should be a reconsideration of hospital policies, and a lower threshold for intervening, an overall survival of about 1 in 5 at 22 weeks about 1 in 3 at 23 weeks (among babies who received active care) would both seem to make intervention more reasonable for more infants; not necessarily for everyone, as always, family values and wishes are extremely important in these decisions, but as survival improves, it makes sense that our willingness to try for survival should also improve.

The most encouraging thing about these data is that there is no evidence at all that increased survival increases the proportion of impairment among survivors, with the limitations of the data presented, the opposite is much more likely to be true.

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Fluid restriction to prevent BPD?

In response to my previous post, one of the comments was a question about fluid volumes in the first few days of life, and whether fluid and/or sodium intake was important for the development of BPD during the early neonatal transition.

In response I will share a slightly edited preprint version of a section of an article I published in Seminars in Perinatology a couple of years ago. Barrington KJ. Management during the first 72h of age of the periviable infant: An evidence-based review. Seminars in Perinatology. 2014;38(1):17-24.

Even though it is a couple of years old, I don’t think there are new RCTs addressing the issues that I reviewed in this section. That article also had sections on cardiovascular support, respiratory management, nutrition, neurologic interventions, protocolized care and research networks.

Also it is important to note that the “systematic reviews” were performed according to the usual standards, but they do NOT conform to the PRISMA guidelines. With the limited space available I couldn’t have done that.

Fluids, electrolytes and renal function

Renal vascular resistance is high immediately after birth, and falls rapidly in the first 24 hours. This fall is associated with a major increase in glomerular filtration rate, and urine output, which is usually clinically evident as an increasing diuresis by the end of the 1st 24 hours of life. After this transition, preterm renal function is marked by a low ability to excrete a sodium load, but little restriction in maximal water clearance.

There are few studies on which to base a decision regarding total fluid management in the extremely immature newborn (EIN).  The skin of the very immature infant is very permeable, and huge trans-epidermal water losses (TEWL) occur if they are placed in a dry environment, the evaporation of water from the skin of the infant leads to cooling due to the latent heat of vaporisation, and it may be impossible to keep the EIN warm in a dry environment under a radiant heater. Most centers have now moved to placing EINs in incubators, although there is no RCT evidence that this is preferable to being under a radiant heater, it seems likely to be the case. If a radiant heater is used it must be combined with an arrangement to keep the humidity around the infant at a high concentration, such as covering the infant with plastic.

One problem with keeping EINs in a high humidity environment is that whenever they are accessed to give care (for example by opening the incubator portholes) the humidity drops precipitously. This is even more evident when the ‘roof’ of an incubator with a retractable cover is lifted. Therefore further methods to reduce trans-epidermal water loss have been examined, including using ointments or semi-permeable membranes. Ointments such as Aquaphor can reduce trans-epidermal water loss, but whether they can improve overall water balance or improve clinical outcomes is uncertain. The only large study in ELBW infants enrolled infants (500 to 1000 g birth weight) starting at an average of about 24 hours of age, and showed an increase in late-onset coagulase negative staphylococcal sepsis during prolonged treatment . Maturation of the epithelial barrier after preterm birth occurs rapidly, a briefer period of barrier treatment could potentially have benefits without this risk. Semi-permeable membranes have also been tried, in a small pre-post study TEWL appears to have been reduced, fluid requirements and peak sodium was lower, and there may have been less BPD, (n=69 birth weight <1000g) but there is no data from adequately powered RCTs examining other clinical outcomes.

Total fluid intake

What should the total fluid intake be? Clearly this will depend on overall fluid losses. But the interaction between the physical environment, and subsequent TEWL, and fluid administration requirements has not been well studied. Several studies have randomly compared infants by total volume of fluid administered. The results are very inconsistent. Those studies have varied in design, in particular by how sodium intake was controlled.

Although the Cochrane review “Restricted versus liberal water intake for preventing morbidity and mortality in preterm infants” suggests that restricted fluid intake improves several clinical outcomes, this result is marked by significant heterogeneity, also one of the better studies did not enrol babies until the 3rd day of life, and therefore is of little relevance to the current review. After the initial period of adaptation as mentioned above, the preterm kidney has a relatively good ability to clear a fluid load. Thus there is little reason to hypothesize that variation in total free water administration, within reasonable limits, will affect total body water.

One of the 5 trials of water restriction gave fluids with identical sodium concentrations in each 100mL of the intravenous fluid, another was designed to examine a relatively complex protocol allowing either 10% or 15% body weight loss and therefore varied both water and sodium intakes. These 2 studies were therefore studies of combined sodium and water restriction.

I have performed a systematic review of RCTs of different fluid administration rates starting on the first day of life, which I have meta-analyzed using the RevMan software, fixed effects model. I found 5 controlled trials (a table showing the articles is at the bottom of this post, followed by a list of references), 3 of which had similar sodium intakes in each group, 2 varied both the fluid and the sodium intake.

Figure 1.Effects of varying fluid intakes on mortality.

figure-1-fluid-restriction

As can be seen, the studies with varying water intake, but no difference in sodium intake showed no effect on mortality, whereas those which varied both showed a reduction in mortality with restricted water and sodium intake. Of note this second result is largely the result of a single trial with a very high mortality in the high water/high sodium group, and this subgroup shows substantial heterogeneity, an I2 of 72%.

Figure 2. Effects of varying fluid intakes on BPD

forest-plot

Clearly there is no effect on BPD, RR 0.93 (95% CI 0.68, 1.27). Survival without BPD was also not different overall.

Sodium intake

In contrast the preterm kidney has a limited ability to excrete a sodium load, and excessive sodium administration may lead to increases in total body water and increases in water content of vital tissues. This is true even though there is a natriuresis in the first few days of life, at least after the first 24 hours, which accompanies the postnatal diuresis. Administration of sodium during this period may well upset the postnatal progressive decrease in extra-cellular fluid which is a normal phenomenon in more mature infants.

I performed a systematic review and meta-analysis of RCTs in preterm infants which compared 2 regimes of sodium administration starting on the first day of life (see the table below). The search found 5 studies, two of which are as mentioned also studies of varying water intake and are mentioned above, and one with very limited description of clinical outcomes (other than death). The total numbers of infants in these trials is a disappointing 271. Nevertheless there appears to be a reduction in mortality RR 0.44 [95% CI 0.22, 0.90] with reduced sodium intake, a possible reduction in BPD, RR 0.76 [95% CI 0.56, 1.04] and a reduction in the combined outcome of death or BPD, RR 0.39 [95% CI 0.23, 0.67].

Figure 3. Effects of different sodium intakes on A. mortality, B. Bronchopulmonary Dysplasia, and C. combined outcome of death or BPD.

figure-2-sodium

The data are therefore probably best interpreted as showing that delaying all sodium intake until after either 3 days of life or after a 5% weight loss improves outcomes whereas restricting free water intake by itself has little or no effect. The major limitation of these data being that very few extremely immature babies have been included in any of these studies.

Table Randomized trials comparing 2 levels of fluid intake or 2 levels of sodium administration in the preterm.

Study ID
n
Characteristics of included infants
Comparison, fluid intakes
Sodium intakes
Primary Outcome
Tammela9
100
<1751 g BW, >23 wk
50,60,70,80,90,100,120 then 150 ml/kg/d vs
80,100,120,150 then 200 ml/kg/d
3 mM/100 mL Na in all the fluids
BPD
Lorenz12
88
750-1500 g BW, day 1 of life
Designed for 10% birth weight loss vs 15%, initially
1,000-1,500g 70 ml/kg/d 750-1,000g 80 ml/kg/d. Thereafter varied according to weight loss.
Higher in high fluid group, 1 mM/kg/d on day 1 increasing to 3 in high fluid group or decreasing to 0.5 in low fluid group, by day 4
No clear primary outcome
Von Stockhausen13
56
Premature, day 1 of life
60 mL/kg/d vs 150 mL/kg/d for 3 days
unclear
No clear primary outcome
Kavvadia14
168
<1501 g BW, day 1 of life
70 increasing to 150 by day 6, 40 increasing to 150 by day 7
Adjusted to achieve serum concentration of 135 to 145 mM/100mL, no difference between groups
Survival without BPD
Costarino15
17
<1000g, <29wk, day 1 of life
Individualized, not different overall  between groups
0 vs 3 to 4 mM/kg/d
Risk of hypernatremia and large fluid volumes
Hartnoll16
46
25 to 30 wk with RDS
Individualized, not different between groups
4 mM/kg/d starting on day 2 vs 0 until weight decreased by 6%
Risk of continuing oxygen dependency
Ekblad11
20
<35 wk
50 increasing to 110 in each group
0 increasing to 2, vs 4 mM/kg/d
No clear primary outcome

References

  1. Lorenz JM, Kleinman LI, Ahmed G, Markarian K. Phases of fluid and electrolyte homeostasis in the extremely low birth weight infant. Pediatrics. 1995;96(3 Pt 1):484-9.
  2. Pabst RC, Starr KP, Qaiyumi S, Schwalbe RS, Gewolb IH. The effect of application of aquaphor on skin condition, fluid requirements, and bacterial colonization in very low birth weight infants. J Perinatol. 1999;19(4):278-83.
  3. Knauth A, Gordin M, McNelis W, Baumgart S. Semipermeable polyurethane membrane as an artificial skin for the premature neonate. Pediatrics. 1989;83(6):945-50.
  4. Nopper AJ, Horii KA, Sookdeo-Drost S, Wang TH, Mancini AJ, Lane AT. Topical ointment therapy benefits premature infants. The Journal of pediatrics. 1996;128(5 Pt 1):660-9.
  5. Edwards WH, Conner JM, Soll RF, for the Vermont Oxford Network Neonatal Skin Care Study Group. The Effect of Prophylactic Ointment Therapy on Nosocomial Sepsis Rates and Skin Integrity in Infants With Birth Weights of 501 to 1000 g. Pediatrics. 2004;113(5):1195-203.
  6. Bhandari V, Brodsky N, Porat R. Improved Outcome of Extremely Low Birth Weight Infants with Tegaderm[reg] Application to Skin. 2005;25(4):276-81.
  7. Bell EF, Acarregui MJ. Restricted versus liberal water intake for preventing morbidity and mortality in preterm infants. Cochrane database of systematic reviews (Online). 2008(1):CD000503.
  8. Bell EF, Warburton D, Stonestreet BS, Oh W. Effect of fluid administration on the development of symptomatic patent ductus arteriosus and congestive heart failure in premature infants. The New England journal of medicine. 1980;302(11):598-604.
  9. Tammela OKT, Koivisto ME. Fluid restriction for preventing bronchopulmonary dysplasia? Reduced fluid intake during the first weeks of life improves the outcome of low-birth-weight infants. Acta Paediatr. 1992;81:207-12.
  10. Drukker AMDP, Guignard J-PMD. Renal aspects of the term and preterm infant: a selective update. Current Opinion in Pediatrics. 2002;14(2):175-82.
  11. Ekblad H, Kero P, Takala J, Korvenranta H, VÄLimÄKi I. Water, Sodium and Acid-Base Balance in Premature Infants: Therapeutical Aspects. Acta Pædiatrica. 1987;76(1):47-53.
  12. Lorenz JM, Kleinman LI, Kotagal UR, Reller MD. Water balance in very low-birth-weight infants: relationship to water and sodium intake and effect on outcome. The Journal of pediatrics. 1982;101(3):423-32.
  13. Stockhausen H, Struve M. Die Auswirkungen einer stark unterschiedlichen parenteralen Flüssigkeitszufuhr bei Früh- und Neugeborenen in den ersten drei Lebenstagen. Klinische Pädiatrie. 2008;192(06):539-46.
  14. Kavvadia V, Greenough A, Dimitriou G, Hooper R. Randomised trial of fluid restriction in ventilated very low birthweight infants. Archives of disease in childhood Fetal and neonatal edition. 2000;83:F91-F6.
  15. Costarino ATJ, Gruskay JA, Corcoran L, Polin RA, Baumgart S. Sodium restriction versus daily maintenance replacement in very low birth weight premature neonates: a randomized, blind therapeutic trial The Journal of pediatrics. 1992;120(1):99-106.
  16. Hartnoll G, Betremieux P, Modi N. Randomised controlled trial of postnatal sodium supplementation on oxygen dependency and body weight in 25-30 week gestational age infants. Arch Dis Child Fetal Neonatal Ed. 2000;82(1):F19.
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Fluid restriction as treatment for BPD? This time with the summary of findings table.

I realize that many of my gentle readers may not have access to the Cochrane reviews in full text as soon as they are published. The NICHD do provide free access to the neonatal reviews, (together with a useful introduction to the value, limitations and methodology of the Cochrane reviews) but it seems to take a couple of months for them to catch up with a new review arriving. Even OVID, one of the ways of accessing some of the Wiley content, which is how I access the reviews from my university, hasn’t updated the Cochrane Library to include the fluid restriction review yet. Which means I can’t even access the full text on-line myself yet!

I will re-post about the 3 latest reviews that we have published as soon as full text is available from the NICHD web-site.

I thought therefore I would re-post this, about the fluid restriction SR, and add a slightly edited version of the Summary of Findings table, with the secondary outcomes of the systematic review that we included. You will note that I could not calculate the confidence intervals for the duration of oxygen therapy, the standard deviations weren’t included in the original article (rather they included the ranges). Nevertheless the means are so similar that the confidence intervals are likely to be wide, and certainly to be ‘not significant’.

fluid-restriction

I have never been convinced that fluid restriction is a good thing for kids with BPD. I think the common practice came about because of the short-term improvements in lung function that sometimes follow if you start diuretics. The idea being that if diuretics improve lung function, then giving less fluid will also.

But this is a false equivalency, diuretics cause sodium depletion, and therefore decrease total body water, and probably lung water content also. Fluid restriction in contrast leads to a reduction in urine output, and, within clinically reasonable limits, will not have an impact on total body water, and there is no reason to believe that they will reduce lung water content either.

Diuretics may have other direct effects on pulmonary function, that will not occur with fluid restriction. Inhaled furosemide, for example, improves pulmonary mechanics in BPD, presumably by acting on the same sort of ion pump that loop diuretics block in the kidney.

Even in adults with fluid overload (those with oedematous congestive heart failure) RCTs of fluid restriction show no effect, unless sodium intake is also severely restricted. Sodium restriction alone works as well, so the fluid restriction adds nothing.

Despite this, there are recommendations from usually reliable people that babies with BPD should have their fluid intake restricted, such recommendations are often accompanied by a reference, usually a reference to another recommendation or to a narrative-type review article.

I have been planning for years to do a systematic review for the Cochrane library, of fluid restriction as treatment for early or established BPD. We have finally finished the review and it has just appeared. (Barrington KJ, Fortin-Pellerin E, Pennaforte T. Fluid restriction for treatment of preterm infants with chronic lung disease. Cochrane Database of Systematic Reviews. 2017(2).)

Using the usual search procedures we could only find one relevant trial. In fact the initial search didn’t find the article (Fewtrell MS, et al. Randomized trial of high nutrient density formula versus standard formula in chronic lung disease. Acta Paediatrica. 1997;86(6):577-82.) even though I knew it existed; the Pubmed key words did not mention fluid volumes or restriction, so we tweaked the search to ensure that we found the article, and to make sure that we would find any others that exist.

So the only RCT evidence addressing fluid restriction is a study of 60 preterm babies with early chronic lung disease (needing oxygen at 28 days of age) who were randomized to either get 180 mL/kg/day of a regular formula, or 145 mL/kg/d of a concentrated formula. Unfortunately they didn’t report on one of our outcomes, oxygen requirement at 36 weeks, as it wasn’t, at that time, the standard outcome that it has since become.

That study showed no benefit of fluid restriction on any outcome. The fluid restricted group had more apneas, a finding unlikely to be due to chance, and also had more babies who needed more than 30% oxygen during the trial, a difference which may have been due to chance.

Fluid restriction risks nutritional restriction also; even though the idea may be to reduce the free water intake, babies often get fewer calories and less protein when fluid restricted, while babies with BPD actually need more calories. They will also produce more concentrated urine, which might increase the risk of nephrocalcinosis as well.

The final message is that there is no evidence to support the practice of fluid restriction of babies with early or established BPD. There is no physiologic rationale either. There are potential risks to the practice.

We should stop doing it.

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