Behavioral Interventions for Infant Sleep Problems: A Randomized Controlled Trial

This paper suggests that controlled crying does not result in any detrimental impact on either the infant or the parents but I feel that the methods and the subsequent conclusions as reported disallow this assumption.
Firstly there are concerns about cortisol measurement. Cortisol is a physiological marker used to measure levels of stress [1]. Two studies [2, 3] have measured cortisol in sleep interventions and the findings were conflicting. Measuring cortisol in infants is fraught with difficulty because normative data are imprecise [4] - cortisol has an intrinsic and variable circadian rhythm [4], particularly in such young babies [4] where cortisol levels are less stable than in older children on which Gradisar et al’s assumptions are based. Presumably the authors were assessing if cortisol would rise from pre-intervention to post-intervention within each child due to the stress of crying alone, yet no individual data is reported to inform if any child actually showed an increase. Furthermore, there is no information or rationale about when and under what circumstances the pre-cortisol measures were taken nor why cortisol was measured one week later. Surprisingly, the authors did not measure cortisol at the time of the stress itself, when the infant was crying unattended. Data [5] show a spike in cortisol in infants soon after 25 minutes after a stressful event (e.g. a finger prick [5] and it may have been more beneficial to test cortisol levels immediately after the stressor of crying unattended. It is difficult to attribute with confidence that stress as measured by cortisol was unaffected one week later particularly as there were reported measure of extraneous stressors during that week. So I argue that cortisol measurements taken in this study are at best unhelpful.
Secondly, given that attachment theorists suggest that not responding to an infant’s crying could promote learned helplessness in some children [6] this team used the Strange Situation Procedure to test if attachment between mother /child was impacted during controlled crying. However, they tested it 6 months after implementing the controlled crying intervention whilst not controlling for any other factors that may (or may not) have impacted attachment between each mother/child dyad and there was no baseline measure of attachment. The authors’ claim that these results support the null hypothesis, but this claim is not possible without controlling for all other factors in the family environments particularly in a sample of just 43 children. Indeed on a sample of 43 children and even less within each group, statistical significance does not provide robust evidence of significance or for that matter non significance, and as such claims would be better presented as preliminary. So I would argue that this data makes it impossible to deduct that controlled crying does or does not impact attachment or stress and therefore the assumptions of this study should be reported as such.
REFERENCES

1. Capaldi, V., et al., Associations between sleep and cortisol responses to stress in children and adolescents: a pilot study. Behavioural Sleep Medicine, 2012. 3(4): p. 177-192.
2. Middlemiss, W., Granger, DA, Goldberg, WA, Nathans, L., Asynchrony of mother-infant hypothalamic-pituitary-adrenal axis activity following extinction of infant crying responses induced during the transition to sleep. Early Human Development, 2012. 88: p. 227-232.
3. Price, A., Wake, M, Ukoumumme, O, Hiscock, H., Five year follow up of harms and benefits of behavioural infant sleep intervention: randomized trial. Pediatrics, 2011. 130(4): p. 643-651.
4. Tollenaar, M.S., et al., Cortisol in the first year of life: Normative values and intra-individual variability. Early Human Development, 2010. 86(1): p. 13-16.
5. Ramsay, D. and M. Lewis, Reactivity and regulation in cortisol and behavioral responses to stress. Child development, 2003. 74(2): p. 456-464.
6. Ainsworth, M., Biehar, MC, Waters, E, Wall, S. , Patterns of attachment: a psychologicalstudy of the strange situation. . 1978, New York: Psychology Press.

The author has no conflict of interest to declare in regards to this manuscript

This paper suggests that controlled crying does not result in any detrimental impact on either the infant or the parents but I feel that the methods and the subsequent conclusions as reported disallow this assumption.
Firstly there are concerns about cortisol measurement. Cortisol is a physiological marker used to measure levels of stress [1]. Two studies [2, 3] have measured cortisol in sleep interventions and the findings were conflicting. Measuring cortisol in infants is fraught with difficulty because normative data are imprecise [4] - cortisol has an intrinsic and variable circadian rhythm [4], particularly in such young babies [4] where cortisol levels are less stable than in older children on which Gradisar et al’s assumptions are based. Presumably the authors were assessing if cortisol would rise from pre-intervention to post-intervention within each child due to the stress of crying alone, yet no individual data is reported to inform if any child actually showed an increase. Furthermore, there is no information or rationale about when and under what circumstances the pre-cortisol measures were taken nor why cortisol was measured one week later. Surprisingly, the authors did not measure cortisol at the time of the stress itself, when the infant was crying unattended. Data [5] show a spike in cortisol in infants soon after 25 minutes after a stressful event (e.g. a finger prick [5] and it may have been more beneficial to test cortisol levels immediately after the stressor of crying unattended. It is difficult to attribute with confidence that stress as measured by cortisol was unaffected one week later particularly as there were reported measure of extraneous stressors during that week. So I argue that cortisol measurements taken in this study are at best unhelpful.
Secondly, given that attachment theorists suggest that not responding to an infant’s crying could promote learned helplessness in some children [6] this team used the Strange Situation Procedure to test if attachment between mother /child was impacted during controlled crying. However, they tested it 6 months after implementing the controlled crying intervention whilst not controlling for any other factors that may (or may not) have impacted attachment between each mother/child dyad and there was no baseline measure of attachment. The authors’ claim that these results support the null hypothesis, but this claim is not possible without controlling for all other factors in the family environments particularly in a sample of just 43 children. Indeed on a sample of 43 children and even less within each group, statistical significance does not provide robust evidence of significance or for that matter non significance, and as such claims would be better presented as preliminary. So I would argue that this data makes it impossible to deduct that controlled crying does or does not impact attachment or stress and therefore the assumptions of this study should be reported as such

Infant sleep is a largely unrevealed, enigmatic phenomenon. Besides advancing the growth of scientific knowledge, the research works focusing on this issue provide support for parents in common everyday life situations. Thus, it is of utmost importance to reliably report the findings on these issues, as well as to consider the relevance of the results and publish figures which do reflect the empirically supported outcomes. In the recent article on behavioral interventions for infant sleep problems (1) data, figures and interpretations diverge significantly. Moreover, authors reach to a conclusion which contradicts their own findings. The presentation of the main findings is biased in the form of the marginalization of objective sleep measures as well as by unnoticing the divergence between objective and parent-reported infant sleep measures.
Objective (actigraphy measured) sleep parameters, including total sleep time and wake after sleep onset do not significantly differ between the treatment groups. This particularly important finding is not emphasized at all in the paper, it is not mentioned in the abstract which might leads to misunderstanding of the results. The titles of the figure 2B and 2D are incorrectly suggesting that treatment effects on sleep are significant. Indeed the figure do not depicts the results on sleep per se, but only the group differences in parental reports. What is a more reliable measure of infant sleep: accelerometry performed by a device attached to the infant’s body surface or the subjective report of the parents perhaps (or most probably) sleeping in a different room?
The interpretation of the findings is biased in terms of the cortisol levels as well. Reported data on cortisol levels do not support the interpretations of cortisol-related findings provided by the authors in their paper. There is a significant reduction in the afternoon cortisol levels of the extinction group, which could reflect the stress from the previous night (very similar to the autoregulatory response seen in the Dexamethasone suppression test (2)). We do not see any data on evening cortisol levels, unfortunately. The authors wrote in the ‘what this study adds’ box that “no significant differences occurred in the infant salivary cortisol”, however we read in the results that “No significant interactions occurred for morning cortisol p > .05 yet there was for afternoon cortisol values, p < .01” and the figure 3B shows this latter significant difference.
Basically the article reports a kind of early separation practice and its consequences. In 2016 it is inevitable to mention the potential epigenetic aspects of these separation procedures. Early maternal separation was shown to alter not only HPA regulation, but the methylation of hypothalamic estrogen receptor genes as well (3). These epigenetic effects can influence multiple aspects of the neurobiology of infant. While considering potential future research directions authors suggest the importance of testing other infant sleeping practices by using a similar approach. In this paragraph authors inappropriately claim that co-sleeping is a risk factor for infant mortality. Indeed several findings support the opposite, including paper published in Pediatrics (4).

References:
1. Gradisar M, Jackson K, Spurrier NJ, et al. Behavioral Interventions for Infant Sleep Problems: A Randomized Controlled Trial. Pediatrics. 2016;137(6):e20151486 doi: 10.1542/peds.2015-1486
2. Carroll BJ. The dexamethasone suppression test for melancholia. The British Journal of Psychiatry. 1982;140:292-304. doi: 10.1192/bjp.140.3.292
3. Weaver ICG, Cervoni N, Champagne FA, et al. Epigenetic programming by maternal behavior. Nature Neuroscience. 2004;7(8):847-54. doi:10.1038/nn1276
4. Mosko A, Richard C, McKenna J, Infant Arousals During Mother-Infant Bed Sharing: Implications for Infant Sleep and Sudden Infant Death Syndrome Research. Pediatrics. 1997;100(5):841-9. doi: 10.1542/peds.100.5.841

I was interested to read the recent work published by Gradisar and colleagues (“Behavioral Interventions for Infant Sleep Problems: A Randomized Controlled Trial”), and its extensive coverage in the media. While the authors are to be commended for evaluating commonly advocated behavioral sleep interventions within a study design that has the potential to actually inform evidence-based recommendations, I have concerns about its ability to meaningfully comment on the safety of any of the interventions studied.

A key claim made (and then propagated more generally within the media), is the apparent safety of the graduated extinction method, described initially in the abstract: “Both graduated extinction and bedtime fading provide significant sleep benefits above control, yet convey no adverse stress responses or long-term effects on parent-child attachment or child emotions and behavior“, yet the authors also note in their power analysis that they would need at least 21 subjects per group to detect a large effect. Given that the largest of the three groups examined comprised 15 subjects, it’s not clear that any meaningful statement can be made about safety, as it appears underpowered to detect even a large effect, let alone a small yet significant one.

Statements made about safety of these interventions form a major part of the widespread public interest in this area, demonstrated by what has been selectively reported in almost every media report referencing this study, yet this is exactly the aspect that is not addressable with this data. While the authors acknowledge the limitations of the small group sizes in the discussion, the emphasis on safety within the article isn’t in proportion to the substance of the finding, and the balance of the communicated message conflates the positive finding, such as reduced sleep latency, with the ability of this study to detect adverse findings in infant stress-response and 12 month attachment, and ultimately, to rationally guide opinion on the safety of the graduated extinction method.