We are pleased to respond to these criticisms of our recently
published paper.
Study integrity
Although we realise our findings may provoke diverse responses to the
much heated debate on bed-sharing we feel it a little unjust to suggest
our findings do not contribute to the scientific literature. We recognised
most of the problems identified by Nishimura and discussed them in the
paper but we strongly object to the conclusion that the results have been
seriously compromised.
Selection bias
We already recognise in the paper the difficulties of recruitment and
although we tried to offset this by introducing weighting by occupational
status this does not rule out the possibility that our random control
families were different from the population by other measures. However the
assumed systematic differences pointed out by Nishimura are naively
constructed and unfounded. The prevalence of habitual alcohol consumption
Nishimura quoted from Public Health Observatory data cannot be directly
compared with our findings as this does not equate to consumption on a
particular night and the population used (South West residents aged 16-64)
is different from population of mothers with dependent children soon
after a birth used in our study. Our findings that only 2% of random
control mothers and 4% of high risk control mothers consumed more than 2
units of alcohol the night before the reference sleep confirms our earlier
findings from a much larger study of England (including the South West
Region with 96% recruitment rate for 1300 control families) where
consumption was 3% amongst the random control mothers.(1) We agree that
alcohol consumption can be under-reported but this would also be true (if
not more so) for the mothers of infants who died. Similarly the 34% of
maternal smokers quoted by Nishimura from a UK survey reported in 2000 is
for mothers who smoke in the year before or during pregnancy. Restricting
the national statistics observation to mothers during pregnancy yields a
prevalence of 19% which fell to 17% by 2005;(2) thus our estimates of 14% is
not that different from the national figure, and may reflect continuation
of the previously reported progressive fall in smoking during pregnancy
over the past decade. The fact that the smoking rates amongst SIDS mothers
is so much higher than even the most deprived control families is not a
reflection of systematic differences but confirms previously reported
observations that this characteristic is just so much more marked amongst
SIDS even when compared to other groups of death amongst families
exhibiting a similar socio-economic profile.(3) The limitation of not
interviewing control families at the weekend was also stated in the paper
along with the fact that when we restricted the analysis to weekdays only
we obtained the same results. Thus although we recognise the possibility
of selection bias we have anticipated this problem where possible in the
study design and tried to address any concerns in the analysis.
Misclassification bias
The depth of investigation included in our study was greater than in
any previously reported study of unexpected infant deaths, with a detailed
clinical history, death scene investigation and thorough post mortem has
been carried out, as well as a multi-disciplinary meeting for every case
to carefully consider the cause of death. On an individual basis it would
be wrong and unfair to attribute accidental death without sufficient
evidence and on a population basis it would be wrong to assume causation
when we only have evidence of an association. In this study we followed
the internationally recognised Avon SUDI classification system. We have
not stated anywhere in the paper that a SIDS baby has died “because a
drunken parent rolled on top of him/her, because a couch cushion
suffocated the baby, or because the baby was unintentionally dropped” and
would hope that US researchers presented with the same evidence would not
make such unjustified assumptions. The mere presence of an infant in a
bed with an adult who had consumed alcohol at the time of the infant death
does not constitute evidence that the death was a direct mechanical
consequence of bedsharing.
Problems with the statistical analysis
We recognise and have reported the limitations due to the smaller
number of deaths in this study and would agree that multicollinearity
could be a problem if we did not already know so much about the variables
we were investigating. However we have conducted similar analyses in
previous larger studies and deliberately used this as a reference to try
and identify major identifiable obvious changes over the last 10 years. We
thought it was clear that the large number of variables tested stems from
our confirmatory intentions to compare our findings with a previous study
rather than an attempt to over extend the present study. At each stage of
the multivariable analysis we have checked for reliability and tried to
concentrate on results that were markedly significant in the univariable
analysis and remained so after the modelling process. We have also been
deliberately cautious in our interpretation of these findings whilst
striving to contextualise the results to build on our previous work.
The chosen population
The fall in the age of SIDS infants is not peculiar to this study,(4)
neither, for that matter is the younger age amongst co-sleeping SIDS
infants.(5) The original Beckwith definition of SIDS does not include an age
range and the 52 week cut-off is somewhat arbitrary, based as much on the
convenience of epidemiological investigation as any dictionary definition
of infancy. The likelihood of an unexplained infant death at 11 months is
not much different to a death at 14 months and in our view the inclusion
of such deaths is equally valid. The inclusion of 3 infants older than 12
months has no bearing on our main findings and we feel is fully justified.
Of course there will be developmental differences but these do not just
manifest at 52 weeks, the one month old infant is very different from the
3 month old and 6 month old infant. Our study includes infants from birth
to 2 years old but the advice for each risk is not generalised to this
group but specific to the infant care practice being investigated.
The findings from our previous study have been instrumental in
influencing risk reduction campaigns not only in the UK but also in the
US. We hope the findings from this study will have a similar impact on
current advice.
References
1. Fleming PJ, Blair PS, Bacon C, Berry PJ. Sudden Unexpected Death
in Infancy. The CESDI SUDI Studies 1993-1996. Pub. The Stationery Office,
London. 2000. ISBN 0 11 322299 8.
3. Leach CEA, Blair PS, Fleming PJ, Smith IJ, Ward Platt M, Berry PJ,
Golding J. Epidemiology of SIDS and explained sudden infant deaths. CESDI
SUDI research group. Pediatrics 1999;104(4).e43
4. Möllborg P, Alm B. Sudden infant death syndrome during low
incidence in Sweden 1997–2005. Acta Paediatr. 2010 Jan;99(1):94-8. Epub .
5. McGarvey C, McDonnell M, Hamilton K, O'Regan M, and Matthews T. An
8 year study of risk factors for SIDS: bed-sharing versus non-bed-sharing.
Arch Dis Child 2006 April;91(4):318–323.
Competing interests:
None declared
Competing interests:
No competing interests
19 January 2010
Peter Fleming
professor of infant health and developmental physiology
Peter S Blair, Peter Sidebotham, Carol Evason-Coombe, Margaret Edmonds, Ellen M A Heckstall-Smith
FSID Research Unit, St Michaels Hospital, Bristol BS2 8EG
Rapid Response:
Authors' reply to Nishimura
We are pleased to respond to these criticisms of our recently
published paper.
Study integrity
Although we realise our findings may provoke diverse responses to the
much heated debate on bed-sharing we feel it a little unjust to suggest
our findings do not contribute to the scientific literature. We recognised
most of the problems identified by Nishimura and discussed them in the
paper but we strongly object to the conclusion that the results have been
seriously compromised.
Selection bias
We already recognise in the paper the difficulties of recruitment and
although we tried to offset this by introducing weighting by occupational
status this does not rule out the possibility that our random control
families were different from the population by other measures. However the
assumed systematic differences pointed out by Nishimura are naively
constructed and unfounded. The prevalence of habitual alcohol consumption
Nishimura quoted from Public Health Observatory data cannot be directly
compared with our findings as this does not equate to consumption on a
particular night and the population used (South West residents aged 16-64)
is different from population of mothers with dependent children soon
after a birth used in our study. Our findings that only 2% of random
control mothers and 4% of high risk control mothers consumed more than 2
units of alcohol the night before the reference sleep confirms our earlier
findings from a much larger study of England (including the South West
Region with 96% recruitment rate for 1300 control families) where
consumption was 3% amongst the random control mothers.(1) We agree that
alcohol consumption can be under-reported but this would also be true (if
not more so) for the mothers of infants who died. Similarly the 34% of
maternal smokers quoted by Nishimura from a UK survey reported in 2000 is
for mothers who smoke in the year before or during pregnancy. Restricting
the national statistics observation to mothers during pregnancy yields a
prevalence of 19% which fell to 17% by 2005;(2) thus our estimates of 14% is
not that different from the national figure, and may reflect continuation
of the previously reported progressive fall in smoking during pregnancy
over the past decade. The fact that the smoking rates amongst SIDS mothers
is so much higher than even the most deprived control families is not a
reflection of systematic differences but confirms previously reported
observations that this characteristic is just so much more marked amongst
SIDS even when compared to other groups of death amongst families
exhibiting a similar socio-economic profile.(3) The limitation of not
interviewing control families at the weekend was also stated in the paper
along with the fact that when we restricted the analysis to weekdays only
we obtained the same results. Thus although we recognise the possibility
of selection bias we have anticipated this problem where possible in the
study design and tried to address any concerns in the analysis.
Misclassification bias
The depth of investigation included in our study was greater than in
any previously reported study of unexpected infant deaths, with a detailed
clinical history, death scene investigation and thorough post mortem has
been carried out, as well as a multi-disciplinary meeting for every case
to carefully consider the cause of death. On an individual basis it would
be wrong and unfair to attribute accidental death without sufficient
evidence and on a population basis it would be wrong to assume causation
when we only have evidence of an association. In this study we followed
the internationally recognised Avon SUDI classification system. We have
not stated anywhere in the paper that a SIDS baby has died “because a
drunken parent rolled on top of him/her, because a couch cushion
suffocated the baby, or because the baby was unintentionally dropped” and
would hope that US researchers presented with the same evidence would not
make such unjustified assumptions. The mere presence of an infant in a
bed with an adult who had consumed alcohol at the time of the infant death
does not constitute evidence that the death was a direct mechanical
consequence of bedsharing.
Problems with the statistical analysis
We recognise and have reported the limitations due to the smaller
number of deaths in this study and would agree that multicollinearity
could be a problem if we did not already know so much about the variables
we were investigating. However we have conducted similar analyses in
previous larger studies and deliberately used this as a reference to try
and identify major identifiable obvious changes over the last 10 years. We
thought it was clear that the large number of variables tested stems from
our confirmatory intentions to compare our findings with a previous study
rather than an attempt to over extend the present study. At each stage of
the multivariable analysis we have checked for reliability and tried to
concentrate on results that were markedly significant in the univariable
analysis and remained so after the modelling process. We have also been
deliberately cautious in our interpretation of these findings whilst
striving to contextualise the results to build on our previous work.
The chosen population
The fall in the age of SIDS infants is not peculiar to this study,(4)
neither, for that matter is the younger age amongst co-sleeping SIDS
infants.(5) The original Beckwith definition of SIDS does not include an age
range and the 52 week cut-off is somewhat arbitrary, based as much on the
convenience of epidemiological investigation as any dictionary definition
of infancy. The likelihood of an unexplained infant death at 11 months is
not much different to a death at 14 months and in our view the inclusion
of such deaths is equally valid. The inclusion of 3 infants older than 12
months has no bearing on our main findings and we feel is fully justified.
Of course there will be developmental differences but these do not just
manifest at 52 weeks, the one month old infant is very different from the
3 month old and 6 month old infant. Our study includes infants from birth
to 2 years old but the advice for each risk is not generalised to this
group but specific to the infant care practice being investigated.
The findings from our previous study have been instrumental in
influencing risk reduction campaigns not only in the UK but also in the
US. We hope the findings from this study will have a similar impact on
current advice.
References
1. Fleming PJ, Blair PS, Bacon C, Berry PJ. Sudden Unexpected Death
in Infancy. The CESDI SUDI Studies 1993-1996. Pub. The Stationery Office,
London. 2000. ISBN 0 11 322299 8.
2. National Statistics. Statistics on Smoking, England 2008 [NS],
October 16 2008, Table 2.12. http://www.ic.nhs.uk/pubs/smoking08
3. Leach CEA, Blair PS, Fleming PJ, Smith IJ, Ward Platt M, Berry PJ,
Golding J. Epidemiology of SIDS and explained sudden infant deaths. CESDI
SUDI research group. Pediatrics 1999;104(4).e43
4. Möllborg P, Alm B. Sudden infant death syndrome during low
incidence in Sweden 1997–2005. Acta Paediatr. 2010 Jan;99(1):94-8. Epub .
5. McGarvey C, McDonnell M, Hamilton K, O'Regan M, and Matthews T. An
8 year study of risk factors for SIDS: bed-sharing versus non-bed-sharing.
Arch Dis Child 2006 April;91(4):318–323.
Competing interests:
None declared
Competing interests: No competing interests