a Based on current occupation.
b Data indicate frequency within the previous 7 days.
TABLE 1. Characteristics of the “Healthy” Cohort of Individuals Followed Prospectively From Phase 1 to Phase 2 of the Health Study of Nord-Trøndelag County
There was a negative relationship between the total amount of exercise undertaken at baseline and risk of future depression (p=0.001). In contrast, the prevalence of case-level anxiety was similar regardless of the levels of baseline exercise (p=0.21). Logistic regression models of the associations between the total amount of exercise at baseline and later depression and anxiety are displayed in Table 2 . After adjustment for a range of confounders, those who reported undertaking no exercise at baseline had a 44% (95% confidence interval = 17%–78%) increased odds of developing case-level depression compared with those who were exercising 1–2 hours a week. The models presented in Table 2 confirm the lack of any association between baseline exercise levels and later case-level anxiety (p=0.27).
None | 1.69 | 1.39–2.06 | 1.16 | 0.96–1.41 |
Up to 30 minutes | 1.29 | 1.10–1.52 | 1.16 | 0.99–1.35 |
31–59 minutes | 1.14 | 0.96–1.35 | 1.15 | 0.99–1.34 |
1–2 hours | 1.00 | 1.00 | ||
2–4 hours | 1.08 | 0.86–1.35 | 1.20 | 0.98–1.45 |
More than 4 hours | 1.03 | 0.81–1.29 | 1.21 | 0.99–1.48 |
None | 1.53 | 1.25–1.88 | 1.09 | 0.90–1.33 |
Up to 30 minutes | 1.23 | 1.04–1.45 | 1.11 | 0.95–1.29 |
31–59 minutes | 1.12 | 0.95–1.33 | 1.13 | 0.97–1.32 |
1–2 hours | 1.00 | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | 1.18 | 0.97–1.44 |
More than 4 hours | 0.98 | 0.78–1.24 | 1.20 | 0.98–1.47 |
None | 1.47 | 1.19–1.80 | 1.03 | 0.85–1.26 |
Up to 30 minutes | 1.20 | 1.02–1.42 | 1.07 | 0.92–1.25 |
31–59 minutes | 1.11 | 0.94–1.32 | 1.12 | 0.96–1.30 |
1–2 hours | 1.00 | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | 1.18 | 0.97–1.44 |
More than 4 hours | 0.97 | 0.77–1.23 | 1.20 | 0.98–1.47 |
None | 1.52 | 1.24–1.86 | 1.09 | 0.90–1.33 |
Up to 30 minutes | 1.22 | 1.03–1.44 | 1.11 | 0.95–1.29 |
31–59 minutes | 1.12 | 0.95–1.33 | 1.13 | 0.97–1.31 |
1–2 hours | 1.00 | 1.00 | ||
2–4 hours | 1.05 | 0.83–1.32 | 1.18 | 0.97–1.44 |
More than 4 hours | 0.99 | 0.79–1.25 | 1.20 | 0.98–1.47 |
None | 1.44 | 1.17–1.78 | 1.03 | 0.84–1.26 |
Up to 30 minutes | 1.19 | 1.00–1.40 | 1.07 | 0.92–1.25 |
31–59 minutes | 1.11 | 0.94–1.31 | 1.12 | 0.96–1.30 |
1–2 hours | 1.00 | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | 1.18 | 0.97–1.44 |
More than 4 hours | 0.99 | 0.78–1.25 | 1.21 | 0.99–1.48 |
a The correlation between regular exercise and reduced incidence of future depression reached statistical significance (p=0.003).
b The correlation between regular exercise and reduced incidence of future anxiety was not statistically significant (p=0.27).
c Adjusted for age and gender.
d Adjusted for age, gender, marital status, education, and social class.
e Adjusted for sociodemographic characteristics plus cigarette and alcohol use.
f Adjusted for sociodemographic characteristics plus body mass index.
g Adjusted for age, gender, marital status, education, social class, number of cigarettes consumed, alcohol use, and body mass index.
TABLE 2. Prospective Associations Between Total Amount of Exercise at Baseline and Later Depression or Anxiety
There was no evidence of interaction by gender (all p values >0.2) or when stratified by age group (greater than or less than 50 years old, p=0.96) in the association between the total amount of exercise at baseline and later case-level depression or anxiety. A similar significant association was seen between baseline levels of exercise and later depression in those aged less than 50 years (p=0.04) and those aged 50 years and older (p=0.03). As expected, there was a significant correlation between the amount of exercise undertaken at baseline and follow-up (p<0.001).
Visual representations of the dose-response relationship between total exercise at baseline and the odds of later case-level depression are provided in Figure 2 . Most of the protective effect of exercise is realized with relatively low levels of exercise, with no indication of any additional benefit beyond 1 hour of exercise each week. Maximum likelihood ratio tests suggest that an exponential decay model (with decreasing benefit as the total time of exercise increases) was a better fit for the data than a linear model (test for difference between models, p=0.004). The combined population attributable fraction for less than 1 hour of exercise per week was 11.9%. There was no evidence of an interaction by intensity of exercise (p=0.96).
FIGURE 2. Adjusted Odds Ratios (With 95% CIs) for Case-Level Depression at Follow-Up According to the Overall Amount of Exercise Reported at Baseline a
a All odds ratios are adjusted for age, gender, marital status, education, social class, number of cigarettes consumed, alcohol use, and body mass index.
In line with a priori predictions, those who engaged in less exercise at baseline tended to have higher resting pulse, lower levels of perceived social support, and more subthreshold symptoms of depression and anxiety, and they were more likely to develop new-onset physical illnesses over the course of the study (p<0.001). Table 3 demonstrates that three of the four potential mediating pathways considered accounted for some of the observed association: reverse causation, lower levels of perceived social support, and new-onset physical illness. However, each of these modeled pathways explained only a very small proportion of the observed effect, with the majority of the protective effect of exercise remaining unaccounted for by measured factors.
0.004 | |||
None | 1.44 | 1.17–1.78 | |
Up to 30 minutes | 1.19 | 1.00–1.40 | |
31–59 minutes | 1.11 | 0.94–1.31 | |
1–2 hours | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | |
More than 4 hours | 0.99 | 0.78–1.25 | |
0.04 | |||
None | 1.40 | 1.13–1.73 | |
Up to 30 minutes | 1.13 | 0.96–1.34 | |
31–59 minutes | 1.07 | 0.90–1.26 | |
1–2 hours | 1.00 | ||
2–4 hours | 1.09 | 0.86–1.37 | |
More than 4 hours | 1.07 | 0.85–1.36 | |
0.002 | |||
None | 1.48 | 1.20–1.82 | |
Up to 30 minutes | 1.21 | 1.02–1.43 | |
31–59 minutes | 1.12 | 0.95–1.33 | |
1–2 hours | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | |
More than 4 hours | 0.98 | 0.78–1.24 | |
0.007 | |||
None | 1.42 | 1.15–1.76 | |
Up to 30 minutes | 1.18 | 1.00–1.40 | |
31–59 minutes | 1.11 | 0.94–1.31 | |
1–2 hours | 1.00 | ||
2–4 hours | 1.04 | 0.83–1.31 | |
More than 4 hours | 0.98 | 0.78–1.24 | |
0.02 | |||
None | 1.38 | 1.11–1.71 | |
Up to 30 minutes | 1.16 | 0.98–1.37 | |
31–59 minutes | 1.09 | 0.92–1.30 | |
1–2 hours | 1.00 | ||
2–4 hours | 1.02 | 0.81–1.29 | |
More than 4 hours | 0.97 | 0.76–1.22 |
a Postestimation was conducted using the Wald test.
b Adjusted for age, gender, marital status, education, social class, number of cigarettes consumed, alcohol use, and body mass index.
c Adjusted for sociodemographic characteristics (as in Model 1) plus baseline symptoms using the 12-item Anxiety and Depression Symptom Index.
d Adjusted for sociodemographic characteristics (as in Model 1) plus resting pulse.
e Adjusted for sociodemographic characteristics (as in Model 1) plus likelihood of support and perceived support from family, friends, or neighbors.
f Adjusted for sociodemographic characteristics (as in Model 1) plus new-onset physical illness.
g The sum of new diagnoses and the level of new impairment were added as separate variables.
TABLE 3. Additional Multivariable Models to Investigate Possible Mediating Pathways Between Total Amount of Exercise at Baseline and Later New Case-Level Depression
Using a large population cohort study, we have observed that relatively small amounts of exercise can provide significant protection against future depression but not anxiety. This protective effect was seen equally across all groups, regardless of the intensity of exercise that was undertaken or the gender or age of the participants. Assuming there is no residual confounding in our final model and the observed relationship is causal, our results suggest that if all participants had exercised for at least 1 hour each week, 12% of the cases of depression at follow-up could have been prevented.
The key strengths of this study are its large sample size, prospective data collection, use of validated measures of physical activity and mental disorder, and the detailed information available on a wide range of potential confounding and mediating factors. Despite these strengths, the analyses presented have some important limitations. Regarding the study design, while individuals reporting current symptoms and/or impairment of depression or anxiety at baseline were excluded using a two-step process, we were not able to exclude individuals with a history of prior episodes of depression and anxiety. Thus, it is possible that some individuals with a lifetime history of depression or anxiety may have been included in the “healthy” cohort, and thus a proportion of the future cases may be recurrent episodes of depression or anxiety. While the long follow-up time is a strength, the use of a single measure of a relapsing and remitting condition such as depression means that some misclassification will have occurred. Such misclassification is likely to be random and therefore results in regression dilution bias and an attenuation of effect sizes. This has important consequences for the interpretation of the results and suggests that the actual protective effect of exercise may be even greater than that reported in this study. The measurement of exercise at a single time point will also have created some misclassification, although there was a significant correlation between levels of exercise at baseline and follow-up. The majority of other limitations relate to the measures used. While the Hospital Anxiety and Depression Scale is one of the most widely used and validated measures of depression and anxiety, the operationalization of any mental disorder via a self-report screening tool cannot be considered equivalent to a clinical diagnosis, and a risk of misclassification remains. Similarly, while the measures of exercise used have been extensively validated ( 30 ), they remain reliant on self-report, and each factor considered in the analysis of mediation was measured with a single item that may not have fully captured the constructs being considered. In addition to standard regression, population attributable fractions were used to describe the relative importance of exercise as a possible preventative strategy. Population attributable fractions can be a useful way to help guide public health interventions, but any estimates of population attributable fractions assume a causal relationship with no residual confounding. While attempts were made to account for many confounders, a number of important potential confounding variables, such as personality, attitude toward health, diet, seasonal weather variations, and the degree to which each participant’s local environment is conducive to regular exercise, remained unmeasured. Nord-Trøndelag County is situated between northern latitudes 63° and 65°. As a result, there is considerable seasonal variation in the number of daylight hours. Previous studies have shown an associated seasonal variation in depression prevalence within Nord-Trøndelag County, with higher rates of depression between December and April ( 36 ). If rates of physical activity were also lower in the winter months, then the confounding effect of the season at the time of assessment could affect any observed cross-sectional association between exercise and depression. However, this longitudinal study mitigates against this by the fact that there was no link between the seasonal timing of the assessments in HUNT 1 (when exercise levels were measured) and HUNT 2 (when levels of depression were assessed). The invitation for participation in the HUNT 2 phase was sent to all residents of the county at a time that was unrelated to when each individual had been assessed during the HUNT 1 phase. The equal popularity of both winter and summer sports in Norway may also have reduced the possibility of seasonal confounding.
This study represents, to our knowledge, the largest and most detailed modeling of the prospective dose-response relationship between exercise and depression and the first published epidemiological exploration of the causal pathways involved. In addition to confirming that more active individuals are less likely to develop depression, we were able to demonstrate that this was most accurately modeled as an exponential decay model, with decreasing benefit as the total time spent exercising increases. This supports and expands on the tentative conclusions from a review published in 2014, which highlighted that substantial mental health benefits may be gained from relatively moderate levels of exercise ( 37 ). Importantly, the majority of the protective effects of exercise against depression are realized within the first hour of exercise undertaken each week, which provides some clues regarding causation and has major implications for possible future public mental health campaigns. The majority of studies examining the role of physical activity in preventing cardiovascular disease have found that the beneficial cardiovascular effects continue to increase up to around 2–3 hours of exercise per week ( 38 , 39 ). Thus, while there are similarities in the overall shape of the dose-response relationship between exercise and depression and exercise and somatic illness, the level of activity needed to realize the bulk of the possible protective effects are very different. Our finding that more vigorous-intensity exercise had no additional protective effects against future case-level depression is also in contrast to previous findings regarding protective factors against cardiovascular disease ( 39 ).
Taken together, these results suggest that processes such as alterations in autonomic nervous system activity and modification of metabolic factors, which require more regular or strenuous exercise, may be less important when considering the protective effects of exercise against future depressive illness. In keeping with this hypothesis, our results suggest that the perceived social benefits of exercise may mediate some of the protective effects against depression. However, within our analysis, the increased levels of perceived social support accounted for only a small proportion of the effect observed, meaning the bulk of the observed protective effect remains unexplained. People’s perception of their social support may be subject to bias relating to their current mental state. This type of reporting bias could lead to an overestimate of the mediating effect of perceived social support, meaning an even greater proportion of the observed protective effect of exercise may be unexplained. We propose two possible explanations to account for the unexplained protective effect of exercise. Firstly, the remaining prospective associations may be due to confounding from factors not measured, such as shared genetic factors, personality, or individual attitudes toward health ( 40 ). Secondly, or alternatively, there may be other causal factors not measured in this study, such as changes in self-esteem, serotonin release ( 41 ), increased expression of neuroprotective proteins such as brain-derived neurotropic factor, altered hippocampal neurogenesis, or modifications to the activity levels of the hypothalamic-pituitary-adrenal axis ( 42 ). The lack of any association between exercise and future anxiety disorders suggests that the link between exercise and depression is not merely related to a general increase in mental well-being and is unlikely to involve risk factors shared between depression and anxiety.
Despite the remaining uncertainty regarding causal pathways, the findings presented in this study have important public health implications. There is evidence that the levels of exercise in the general population in developed countries have decreased considerably over the recent decades ( 43 ), with similar trends now also being observed in developing countries. The results of this study indicate that relatively modest increases in the overall amount of time spent exercising per week may be able to prevent a substantial number of new cases of depression. If causality is assumed and there are no other major cofounders, our results suggest that at least 12% of new cases of depression could be prevented if all adults participated in at least 1 hour of exercise each week. While education regarding the higher levels of exercise required to achieve maximum cardiovascular and metabolic benefits remains important, informing individuals that significant mental health benefits may be achieved with small changes in their behavior may be valuable in facilitating behavioral change. Given that the intensity of exercise does not appear to be important, it may be that the most effective public health measures are those that encourage and facilitate increased levels of everyday activities, such as walking or cycling. The results presented in this study provide a strong argument in favor of further exploration of exercise as a strategy for the prevention of depression.
Prof. Mykletun and Dr. Hotopf are joint last authors.
The HUNT study [Health Study of Nord-Trøndelag County] is a collaboration between the HUNT Research Centre, Faculty of Medicine, Norwegian University of Science and Technology (NTNU, Verdal), Norwegian Institute of Public Health and Nord-Trøndelag County Council.
This study represents independent research funded by the National Institute for Health Research (NIHR) Biomedical Research Centre at South London and Maudsley NHS Foundation Trust and King’s College London. The views expressed are those of the author(s) and not necessarily those of the NHS, the NIHR, or the Department of Health. None of the funders had any role in the study design, collection, analysis, interpretation of data, writing of the manuscript, or the decision to submit this study for publication.
A/Prof. Harvey was funded by NSW Health and a grant from the Institute of Social Psychiatry. Prof. Mykletun and Prof. Øverland were funded by the Norwegian Research Council. All other authors report no financial relationships with commercial interests.
The authors thank Erlend Bergesen, who was initially involved in this study but, sadly, died in August 2006.
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Introduction, disclosure statement.
Stephen A Booth, Mary A Carskadon, Robyn Young, Michelle A Short, Sleep duration and mood in adolescents: an experimental study, Sleep , Volume 44, Issue 5, May 2021, zsaa253, https://doi.org/10.1093/sleep/zsaa253
This study examines the relationship between experimentally manipulated sleep duration and mood in adolescents.
Thirty-four adolescents (20 male), aged 15–17 years, lived in a sleep laboratory for 10 days and 9 nights. They were allocated to one of three sleep “doses” for five consecutive nights for 5, 7.5, or 10 h sleep opportunity per night. Two baseline nights and two recovery nights entailed 10 h sleep opportunity per night. Mood was measured every 3 h during wake using unipolar visual analogue scales measuring the mood states “depressed,” “afraid,” “angry,” “confused,” “anxious,” “happy,” and “energetic.”
Mixed models analyses with post hoc comparisons revealed that participants in the 5-h group, but not the 7.5- or 10-h groups, reported being significantly more depressed, angry, and confused during sleep restriction than at baseline. Adolescents were significantly less happy and energetic during sleep restricted to 5 h and significantly less energetic during sleep restricted to 7.5 h. When adolescents had 10 h sleep opportunities their happiness significantly increased. No statistically significant effects of sleep restriction were found for fear or anxiety, although small-to-moderate effects of sleep restricted to 5 or 7.5 h were found. Two nights of recovery sleep was not sufficient to recover from increased negative mood states for the 5-h group, although recovery occurred for positive mood states.
Given the prevalence of insufficient sleep and the rising incidence of mood disorders and dysregulation in adolescents, these findings highlight the importance of sufficient sleep to mitigate these risks.
Adolescence is a critical maturational stage in terms of heightened risk of the onset of mood disorders. Insufficient experimental evidence exists that elucidates the effect of sleep duration on a range of positive and negative mood states in adolescents. The present study uses sleep restriction and sleep extension protocols to experimentally manipulate sleep duration in 34 adolescents. Results indicated that adolescents reported deteriorated in terms of depression, happiness, anger, confusion and energy. Two nights of recovery sleep did not eliminate mood deficits for negative mood states for the 5-h group, although recovery occurred for positive mood states. Sufficient sleep is crucial to guard against mood deficits in otherwise healthy adolescents.
Adolescence is a time of significant psychological, social, and physiological change [ 1 ] and a vulnerable developmental period during which individuals are at heightened risk of developing a mental illness [ 2 ]. Despite the importance of mood and the commonly held belief that sleep loss perturbs adolescent mood [ 3 , 4 ], rigorous experimental evidence supporting a causal relationship between sleep loss and mood deficits in adolescents is scant. The current experiment tests the causal association between sleep duration and adolescent mood.
Empirical literature on sleep duration and mood has overwhelmingly focused on adults [ 5–7 ]; however, adult findings may not generalize to adolescents. Adolescents differ in terms of their greater sleep need [ 8 , 9 ], types of affective challenges they face [ 10 ], and less mature prefrontal brain regions that are crucial to affective regulation [ 11 ]. As such, research focusing specifically on adolescents is needed. Most of the extant literature focusing on sleep duration and mood in adolescents is cross-sectional. These studies report a correlation of sleep duration and mood, with shorter sleep associated with worse mood [ 12 , 13 ]. Due to the cross-sectional nature of such studies, however, a casual relationship cannot be concluded.
A recent study investigated the effect of sleep restriction and sleep extension on a group of 48 adolescents aged 14–17 years with Attention Deficit Hyperactivity Disorder using a 3-week sleep protocol with an experimental crossover design in participants’ homes [ 14 ]. Sleep restriction involved a week with a 6.5 h sleep opportunity per night while sleep extension involved a week of 9.5 h sleep opportunities per night. Parent- and self-reported depressive symptoms were greater during sleep restriction compared to sleep extension, while positive affect was lower. Parents also reported increased negative affect and emotion dysregulation among adolescents during sleep restriction when compared to extension.
Among the limited experimental studies including adolescents, two were performed under continuous monitoring. The sleep of 113 adolescents, aged 15–19 years, was restricted to a 5-h sleep opportunity for seven consecutive nights, with or without a 1-h daytime nap opportunity [ 15 , 16 ]. Mood was assessed three times per day using Positive and Negative Affect Scales (PANAS). Compared to controls, who had 9-h sleep opportunity per night, sleep-restricted adolescents reported significantly lower positive mood scores. The detriment to positive mood was only partially ameliorated by an afternoon nap. Unexpectedly, no change was observed to negative mood. Lo et al. note that adolescents reported that many of the mood states assessed by the PANAS negative mood subscale, such as guilty, afraid, and scared, were not relevant to them [ 15 ]. Differential sensitivity to sleep loss among mood states has been reported in a recent meta-analysis of 361,505 adolescents [ 17 ], with positive mood showing the largest effect in response to shorter sleep (OR = 1.02), followed by anger (OR = .83), depression (OR = .62), and anxiety (OR = .41). The present literature is limited by the paucity of studies that have examined specific mood states [ 18 ]. Other challenges arise in those studies using home-based sleep restriction schedules where breaches of adherence to study protocols regarding sleep and abstinence from napping and caffeine may muddle interpretation [ 19 , 20 ].
The present study addresses the gaps and limitations in current literature by employing a laboratory-based experimental design to measure several discrete mood states over varying “doses” of sleep. The laboratory environment ensures adherence to study protocols and control of environmental variables, such as diet, caffeine consumption, and exercise that are known to affect sleep and mood [ 21–23 ]. The repeated-measures design whereby participants in each condition have their mood compared between baseline, the sleep dose condition, and following recovery sleep provides the opportunity for robust conclusions regarding the causal link between sleep duration and mood.
We hypothesized that self-reported mood will be significantly worse during sleep restriction when compared to extended 10-h baseline and recovery sleep opportunity, with positive moods decreasing and negative moods increasing when sleep is restricted to 5- or 7.5-h sleep opportunity per night, as neither duration allows for sleep that is within the recommended range for adolescents [ 24 ] (i.e. 8–10 h sleep per night).
Participants were 34 adolescents aged 15–17 years (20 male, M age = 15.91 years ± 0.86) from South Australian high schools. All participants were late- or postpubertal adolescents (Tanner Stage 4 or 5 on the Pubertal Development Scale) [ 25 ]. Prescreening by parent and adolescent self-report, showed that participants were physically and psychologically healthy and were medication-free, with the exception of birth control. Participants were good sleepers, with average sleep durations ≥8 h per night [ 26 ], average sleep onset latencies of ≤30 min per night [ 27 ], and weeknight/weekend bedtime discrepancy less than 2 h [ 28 ], as determined by a survey and a 7-day sleep diary during screening, to reduce confounding effects of preexisting poor sleep and/or sleep disorders. Extreme morning or evening chronotypes were not included (≥44 or ≤22 on the Composite Morningness/Eveningness Scale) [ 29 ] due to effects of chronotype on adolescent sleep and mood [ 30 ], nor were participants indicating less than 8 h sleep per night on average, weekend bedtime delay of 2 h or more, or sleep onset latencies greater than 30 min per night.
Mood was measured using a series of 100 mm unipolar visual analog scale (VAS), similar to those used in a study by Stern et al. [ 31 ]. These consisted of scales with labels to demonstrate the spectrum of discrete mood experience, with “Not at all (mood)” at the left endpoint and “Extremely (mood)” on the right endpoint. Mood states included “Depressed,” “Afraid,” “Angry,” “Confused,” “Anxious,” “Happy,” and “Energetic.”
At each test administration, participants were asked to describe how they felt “RIGHT NOW” by marking a short vertical line intersecting the scale at some point, placing the mark further to the right to reflect the greater intensity of that mood. Items were scored by measuring the distance in millimeters from the left anchor of the scale to the point at which the participant intersects the scale with a line. Unipolar scales (i.e. spanning the range of not at all sad to extremely sad, as opposed to bipolar scales which may span happy to sad) were selected as they reduce participant confusion as compared to a bipolar scale [ 31 ].
Sleep was recorded prior to the laboratory experiment with sleep diaries, actigraphy, and by getting participants to call and leave a message on the sleep laboratory answering machine confirming their and waketime. During the laboratory experiment, sleep was recording using nightly polysomnography. Further information regarding sleep measurement is provided elsewhere [ 8 ].
This study used a mixed experimental design. The independent variables were sleep duration dose (5, 7.5, and 10 h groups), and sleep condition (Baseline, Experimental Sleep, and Recovery); dependent variables were the mood terms: “Depressed,” “Afraid,” “Angry,” “Confused,” “Anxious,” “Happy,” and “Energetic.”
An active recruitment process was used to recruit adolescent participants through announcements in South Australian high-school newsletters. Parents of potential participants provided an initial telephone screen using the Sleep, Medical, Educational, and Family History Survey [ 12 ]. Adolescent participants meeting preliminary inclusion criteria were sent a questionnaire package that included a modified Sleep Habits Survey, the Smith Composite Morningness/Eveningness questionnaire, the Pubertal Development Scale and the Sleep, Medical, Education and Family History Survey and a 7-day sleep diary and were invited to attend an interview. Upon confirming eligibility and obtaining parental consent and adolescent assent, adolescents were provided a sleep diary and a wrist activity monitor for the week prior to the in-lab study. Participants were allocated in blocks of four participants to one of the three sleep-dose conditions. Adolescents in each study run were in the same condition and were not informed of their sleep opportunity each night until the end of the study. Adolescents were required to maintain a 9.5 h sleep opportunity between 9:30 pm and 07:00 am for five nights prior to the study to eliminate any existing sleep debt before the start of the study. Thirty-seven participants (21 males) were recruited; however, one did not follow the required pre-study sleep protocol and was excluded from the study and two others (both females assigned to the 7.5 h condition) discontinued their participation before the study’s conclusion.
On the first two of nine consecutive laboratory nights, a 10 h sleep opportunity was provided to extinguish any residual sleep debt and provide baseline sleep and mood data. Adolescents’ polysomnographically estimated sleep durations on the adaptation and baseline nights were not significantly different between conditions (all p < .05). Five experimental nights of 5, 7.5, or 10 h sleep opportunity followed, with wake time at 7:30 am regardless of sleep duration. This wake time was chosen to simulate typical rising early for school, as adolescents generally restrict sleep by staying up late rather than getting up early [ 32 ]. Two recovery nights of 10 h sleep opportunity concluded the experiment. The VAS was administered three-hourly across all wake periods, as shown in Figure 1 .
Schematic of the study protocol, displaying days by hours over three sleep dose conditions.
To control environmental variables, participants completed the study in a laboratory free of time-cues, without access to caffeine or to live television or Internet. Participants had access to mobile phones for one 15-min period each day, although Internet access was disabled and phone clocks were altered. Participants spent their time playing board games, doing craft activities, watching prerecorded movies and television series, and interacting with one another and with research staff. The laboratory was light- (<50 lx during wake periods and <1 lx during sleep opportunities) and temperature- (21 ○ C) controlled and sound-attenuated. Participants’ scheduled sleep episodes were recorded using polysomnography to confirm participant sleep times. Findings regarding changes to sleep and attention variables are reported elsewhere [ 8 ].
Linear mixed-effects models were used to test differences in mood across sleep conditions (baseline, sleep restriction, and recovery) for both males and females. This analytic approach accounted for both within and between-participant variance [ 33 ]. All models specified a random effect of subject ID. Models for mood specified “Depressed,” “Afraid,” “Angry,” “Confused,” “Anxious,” “Happy,” and “Energetic” as dependent variables. Each model was fully saturated, including all main and interaction effects, for sleep dose (5, 7.5, and 10 h), sleep condition (baseline, sleep restriction, and recovery), and sex. Baseline data collected on day 2 were excluded to reduce acclimatization effects as participants adjusted to a novel environment. Cohen’s d was calculated to indicate effect size.
Results are presented for the interactions between sleep dose group (i.e. 5, 7.5, or 10 h) and study phase (baseline, sleep restriction, or recovery) in Tables 1–2 and Figure 2 . Noted differences refer to statistical significance at a p < .05 level. Effect sizes are presented using Cohen’s d , where .2, .5, and .8 indicate a small, medium, and large effect size, respectively.
Inferential statistics for main effects and interactions of sleep dose and sleep condition on negative mood variables
. | . | . | Post hoc . |
---|---|---|---|
Depressed | |||
Dose | 4.08 | .03* | 5 h > 7.5 h, 10 h |
Condition | 4.87 | .008* | RC > BL, ES |
Dose × Condition | 7.64 | <.001* | 5 h: RC > ES > BL |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Afraid | |||
Dose | 4.59 | .02* | 5 h > 7.5 h, 10 h |
Condition | 6.08 | .002* | RC > ES |
Dose × Condition | 7.07 | <.001* | 5 h: RC > BL, ES |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Angry | |||
Dose | 3.82 | .03* | 5 h > 7.5 h, 10 h |
Condition | 1.72 | .18 | |
Dose × Condition | 3.09 | <.001* | 5 h: ES, RC > BL |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Confused | |||
Dose | 2.97 | .07 | |
Condition | 2.71 | .07 | |
Dose × Condition | 4.85 | .001* | 5 h: ES, RC > BL |
7.5 h: no significant differences | |||
10 h: RC > BL, ES | |||
Anxious | |||
Dose | 1.45 | .258 | |
Condition | 40.93 | <.001* | RC > BL, ES |
Dose × Condition | 1.89 | .11 |
. | . | . | Post hoc . |
---|---|---|---|
Depressed | |||
Dose | 4.08 | .03* | 5 h > 7.5 h, 10 h |
Condition | 4.87 | .008* | RC > BL, ES |
Dose × Condition | 7.64 | <.001* | 5 h: RC > ES > BL |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Afraid | |||
Dose | 4.59 | .02* | 5 h > 7.5 h, 10 h |
Condition | 6.08 | .002* | RC > ES |
Dose × Condition | 7.07 | <.001* | 5 h: RC > BL, ES |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Angry | |||
Dose | 3.82 | .03* | 5 h > 7.5 h, 10 h |
Condition | 1.72 | .18 | |
Dose × Condition | 3.09 | <.001* | 5 h: ES, RC > BL |
7.5 h: no significant differences | |||
10 h: no significant differences | |||
Confused | |||
Dose | 2.97 | .07 | |
Condition | 2.71 | .07 | |
Dose × Condition | 4.85 | .001* | 5 h: ES, RC > BL |
7.5 h: no significant differences | |||
10 h: RC > BL, ES | |||
Anxious | |||
Dose | 1.45 | .258 | |
Condition | 40.93 | <.001* | RC > BL, ES |
Dose × Condition | 1.89 | .11 |
Final column displays significant post hoc comparisons ( p < .05). Post hoc comparisons for the main effect of “dose” are between subjects’ comparisons while all remaining comparisons are within-subjects.
Note. BL, baseline sleep condition; ES, experimental sleep dose; RC, recovery sleep condition; 5 h, 5 h experimental sleep dose; 7.5 h, 7.5 h experimental sleep dose; 10 h, control group with 10 h sleep dose.
Inferential statistics for the main effects and interactions of experimental sleep dose and sleep condition on positive mood variables
. | . | . | Post hoc . |
---|---|---|---|
Happy | |||
Dose | 0.93 | .93 | |
Condition | 17.98 | <.001* | RC > BL, ES |
Dose × Condition | 12.12 | <.001* | 5 h: BL, RC > ES |
7.5 h: RC > ES | |||
10 h: RC > ES > BL | |||
Energetic | |||
Dose | 0.56 | .56 | |
Condition | 28.11 | <.001* | BL, RC > ES |
Dose × Condition | 19.84 | <.001* | 5 h: BL, RC > ES |
7.5 h: BL, RC > ES | |||
10 h: no significant differences |
. | . | . | Post hoc . |
---|---|---|---|
Happy | |||
Dose | 0.93 | .93 | |
Condition | 17.98 | <.001* | RC > BL, ES |
Dose × Condition | 12.12 | <.001* | 5 h: BL, RC > ES |
7.5 h: RC > ES | |||
10 h: RC > ES > BL | |||
Energetic | |||
Dose | 0.56 | .56 | |
Condition | 28.11 | <.001* | BL, RC > ES |
Dose × Condition | 19.84 | <.001* | 5 h: BL, RC > ES |
7.5 h: BL, RC > ES | |||
10 h: no significant differences |
Effect sizes (Cohen’s d ) of changes to mood states between baseline and experimental sleep dose for the 5-, 7.5-, and 10-h sleep dose conditions.
Descriptive statistics for all mood states are provided in the Supplementary Material , and inferential statistics with post hoc test results are provided in Table 1 . Figure 2 illustrates the effect size of the changes in mood states between baseline and experimental sleep dose across the three groups. Overall, the change to mood states across the phases of the study (baseline, experimental sleep dose, and recovery) varied between experimental sleep dose groups for depressed mood, anger, and confusion, but not fear or anxiety. Specifically, participants reported greater depressed mood, anger, and confusion during the experimental sleep dose when compared to baseline, but this effect was only seen when sleep was restricted to 5 h TIB and not during the 7.5 h sleep dose. Depressed mood and fear also increased from experimental sleep dose to recovery for participants in the 5 h group. Confusion increased during recovery when compared to baseline and experimental sleep dose for participants in the 10 h group. No significant changes to other mood states were found between experimental sleep dose and recovery in the 7.5 or 10 h sleep groups.
Inferential statistics and post hoc results are provided in Table 2 . The change to mood states across the phases of the study (baseline, experimental sleep dose, and recovery) varied between sleep dose groups for both happiness and energy. Specifically, participants reported significantly reduced happiness when sleep was restricted to 5 h. They also reported significantly less energy when sleep was restricted to either 5 or 7.5 h sleep opportunities per night. Participants’ happiness increased from baseline to experimental sleep dose in the 10 h sleep dose (control group), and there was a small but nonsignificant increase in energy. Significant increases in happiness and energy also occurred between the experimental sleep period and recovery for adolescents in the 5 and 7.5 h sleep dose groups, while happiness increased between the sleep dose phase and recovery for participants in the 7.5 and 10 h groups.
The aim of the current study was to explore the effect of five nights of sleep limited to either a 5, 7.5, or 10 h sleep opportunity per night on adolescent mood, when compared with baseline and recovery conditions which had 10-h sleep opportunities. Consistent with previous research [ 15–17 , 34 ], positive moods of happiness and energy significantly decreased when sleep was restricted to 5 h sleep opportunity per night, with large effect sizes for both moods. This finding is consistent with results found in adult studies that used a VAS to measure mood [ 5 ], establishing the sensitivity of happiness and energy to sleep loss. It is interesting to note that, although obtaining less than the recommended 8–10 h sleep per night [ 24 , 26 ], positive moods only decreased for energy but not happiness in the 7.5 h group, although a small-to-medium effect size was observed. Conversely, happiness, but not energy, increased from baseline to experimental sleep dose in the 10 h control group, suggesting that when adolescents consistently have the opportunity to obtain optimal sleep, happiness increases.
Results regarding negative mood states of depression, fear, anger, confusion, and anxiety were mixed. Participants in the 5 h group were significantly more depressed, angry, and confused when restricted to 5 h TIB compared to baseline, with large effect sizes for all changes. Likewise, extant research has found that depressed mood, anger, and confusion increased in response to less sleep [ 19 , 35 ]. Similar to results found for positive moods, no changes to negative mood states were observed in the 7.5-h group between baseline and experimental sleep dose, despite not obtaining the recommended duration of sleep.
Fear and anxiety did not increase during the experimental sleep phase for adolescents in the 5 or 7.5 h sleep dose groups. Findings in regard to the sensitivty of anxiety to sleep loss have been mixed [ 34 ]. There are several possible explanations for this discrepancy. First, experimental studies have struggled to replicate cross-sectional results linking less sleep to increased negative mood in adolescents [ 18 , 19 ]. A lack of significant findings in some moods may be a result of a differential sensitivity. It is possible that the “dosage” and chronicity of sleep restriction implemented in the current study, as well as previous experimental research, were sufficient to elicit an increase in depressed mood, anger, and confusion in adolescents, but not fear or anxiety. More chronic sleep restriction may be required to find observable effects. It is important to note that while statistical significance was not reached, the effect size for the increase in anxiety from baseline to sleep restriction was medium ( d = .51) for the 5 h group and small ( d = .27) for the 7.5 h group, thus part of this nonsignificant finding may also reflect a lack of statistical power in the current analyses.
Another possible explanation for the lack of a significant relationship between sleep duration and fear and anxiety has been suggested [ 36 ]. It is argued that individual differences can predict mood responses to restricted sleep, such as a phenomenon where stressful life events influence the development of a person’s genes, making them more susceptible to mood disturbances upon reduced sleep. Restricting sleep reduces cognitive resources needed to dismiss negative stimuli, and those susceptible individuals, having biased attention for negativity, become less able to regulate or reappraise them. This is supported by Gregory et al. [ 37 ], who found that the greatest variance in the relationship between sleep duration and anxiety was accounted for by genetic factors. As the participants recruited for the current study underwent an extensive screening process, ensuring physical and psychological health, this may have minimized the possibility that individuals at higher risk of mood and/or sleep disorders would be included. Fuligni et al. have similarly found that adolescents with greater depressed mood and anxiety need more sleep for optimal mood [ 38 ]. Thus, a sample of adolescents with heightened depressed mood or anxiety at baseline may be less resilient to sleep loss. Although literature reporting this effect focuses on depressed mood and anxiety [ 36 , 37 ], it is possible that the same vulnerabilities apply to other mood states, such as fear. As such, the present results may underestimate the effect that sleep loss has on mood states among the general adolescent population.
As seen in the 5 h sleep dose group, positive mood states of happiness and energy significantly increased from sleep restriction to recovery. In addition, the 7.5 h sleep dose group displayed more energy but not happiness between the sleep restriction and recovery phases. These increases in positive mood states following recovery sleep provide support for the restorative effects of optimal sleep following cumulative sleep loss, allowing adolescents mood to recover to baseline values. For the 10 h sleep dose, happiness increased from baseline to the sleep dose condition, then further increased during recovery. This demonstrates that obtaining optimal sleep increases happiness, with 10 h group participants’ self-reported happiness increasing by more than 10% over the course of the study. Larger effects of sleep loss on mood were found for positive mood states, consistent with recent meta-analytic findings in adolescents [ 17 ]. This highlights the importance of considering positive mood states in research into the impact of sleep on mood and also has important clinical ramifications, given the role of anhedonia in psychological disorders such as depression.
It was expected that negative moods would recover from sleep restriction to recovery for participants in the 5 and 7.5 h sleep restriction conditions. Conversely, in the 5 h sleep dose, depressed mood and fear significantly increased from sleep restriction to recovery. It has been suggested that this increase in negative mood may be a natural effect of living in a laboratory environment, as has observed in adult participants given 9 h sleep opportunities over nine nights [ 39 ]. If so, it would be expected that this same pattern would be observed in the 10 h sleep dose group. However, the only mood to demonstrate this effect without sleep loss was confusion. It is possible that the factors leading to increased negative moods in adults placed in a laboratory environment do not affect adolescents in the same way. This may be due to differences in study protocols, or adolescents’ reduced ability to regulate mood following a period of sleep restriction [ 19 ] when faced with a mood-evoking situation (i.e. leaving the laboratory and their new-found friends). As reported elsewhere [ 8 ], salivary dim light melatonin onset showed a significant and dose–response delay in response to sleep restriction. As such, participants in the 5 h condition completed the study with a circadian rhythm that ran nearly 3 h later than it did at baseline. As a result, adolescents were likely to be waking closer to their circadian nadir, which may result in increased sleep inertia and worse mood, even following recovery sleep.
The current study was able to control for many of the confounding factors, which may have influenced the outcomes of prior adolescent sleep research. No other identified adolescent study examining the effect of sleep on mood was completed entirely under laboratory conditions. As such, previous studies were not able to control for exposure to environmental variables and diet, such as caffeine or excessive sugar to the same degree. The laboratory conditions allowed enforced bed/wake times, permitting stronger causal conclusions to be made about the effect of sleep duration on mood without having to consider response biases inflating relationships between subjective sleep and mood measures when both sleep and mood are measured subjectively. However, laboratory conditions present additional challenges, with reduced ecological validity.
Some of the challenges of the laboratory environment in measuring mood outcomes include the effect of an unfamiliar environment, socializing with peers who are not part of their normal friendship groups, and lack of contact with friends and family, which could have been confounding factors in the effect of sleep restriction on mood. It is a possibility that in a more familiar environment, such as participants’ homes, we may expect to see a more ecologically valid indication of the effect of sleep on mood; however, this comes at a cost of greater exposure to extraneous variables. Nonetheless, the inclusion of 7.5 and 10 h sleep dose groups provides a direct comparison between conditions to test the independent effects of sleep “dose” on mood and helps to distinguish between the effects of sleep loss and what may result simply from being in a laboratory environment for an extended period.
An important consideration regarding the current study is that the screening process ensured that participants were both physically and psychologically healthy. Although this is important to minimize exposure to at-risk individuals and to control for confounding variables, it is possible that the sample of the current study was more impervious or resilient to many of the mood disturbances often associated with inadequate sleep. As such, mood effects witnessed in the present study may have been felt more acutely in at-risk individuals, as indicated by prior research [ 36 , 38 ].
Patterns of cumulative sleep loss are increasingly prevalent among adolescents [ 40 ]. The current study found that, when restricted to 5 h sleep for five nights, adolescents’ happiness and energy decreased, depressed mood, anger, and confusion increased, while fear and anxiety did not change. For participants in the 7.5 sleep dose, no significant changes to positive or negative moods were observed between baseline and sleep restriction conditions, and this degree of sleep restriction may require a longer period of time to observe detrimental effects to mood. It is important to note that, while statistical significance was not reached, small-to-medium effect sizes in changes to these mood states were observed between baseline and sleep restriction in the 7.5-h condition. As such, we cannot be sure that, over an extended period of time, that sleep restricted to 7.5 h sleep opportunity per night may not be damaging to mental health.
The implications of the effect of sleep duration on mood relate to the increasing incidence of both sleep loss and mood disorders in adolescents [ 41–43 ], suggesting a greater need for awareness, support, and intervention in promoting healthy sleep for adolescents [ 44 ]. In addition, findings of the current study demonstrate the rapidity of mood decline when adolescent sleep is restricted to 5 h per night, while a more modest amount of sleep loss may require an extended period to see similar effects. Given the prevalence of insufficient sleep and the rising incidence of mood disorders and dysregulation in adolescents, these findings highlight the importance of sufficient sleep to mitigate these risks.
Financial disclosure: The authors have no financial conflicts of interest to declare.
Non-financial disclosure: The authors have no non-financial conflicts of interest to declare.
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There is a growing literature exploring the placebo response within specific mental disorders, but no overarching quantitative synthesis of this research has analyzed evidence across mental disorders. We carried out an umbrella review of meta-analyses of randomized controlled trials (RCTs) of biological treatments (pharmacotherapy or neurostimulation) for mental disorders. We explored whether placebo effect size differs across distinct disorders, and the correlates of increased placebo effects. Based on a pre-registered protocol, we searched Medline, PsycInfo, EMBASE, and Web of Knowledge up to 23.10.2022 for systematic reviews and/or meta-analyses reporting placebo effect sizes in psychopharmacological or neurostimulation RCTs. Twenty meta-analyses, summarising 1,691 RCTs involving 261,730 patients, were included. Placebo effect size varied, and was large in alcohol use disorder ( g = 0.90, 95% CI [0.70, 1.09]), depression ( g = 1.10, 95% CI [1.06, 1.15]), restless legs syndrome ( g = 1.41, 95% CI [1.25, 1.56]), and generalized anxiety disorder ( d = 1.85, 95% CI [1.61, 2.09]). Placebo effect size was small-to-medium in obsessive-compulsive disorder ( d = 0.32, 95% CI [0.22, 0.41]), primary insomnia ( g = 0.35, 95% CI [0.28, 0.42]), and schizophrenia spectrum disorders (standardized mean change = 0.33, 95% CI [0.22, 0.44]). Correlates of larger placebo response in multiple mental disorders included later publication year (opposite finding for ADHD), younger age, more trial sites, larger sample size, increased baseline severity, and larger active treatment effect size. Most (18 of 20) meta-analyses were judged ‘low’ quality as per AMSTAR-2. Placebo effect sizes varied substantially across mental disorders. Future research should explore the sources of this variation. We identified important gaps in the literature, with no eligible systematic reviews/meta-analyses of placebo response in stress-related disorders, eating disorders, behavioural addictions, or bipolar mania.
Introduction.
A placebo is an ‘inactive’ substance or ‘sham’ technique that is used as a control for assessing the efficacy of an active treatment [ 1 ]. However, study participants in a placebo control group may experience considerable symptom improvements - a ‘placebo response’ [ 1 , 2 , 3 ]. Statistical artifacts or non-specific effects account for some of the placebo response. For example, many individuals seek treatment and are enrolled in clinical trials while their symptoms are at their worst. Their symptoms will gradually return to their usual severity (‘regression to the mean’), giving the appearance of a placebo response [ 4 ]. Further, it has been suggested that the placebo response is exacerbated due to unreliable ratings as well as baseline symptom severity inflation if raters are aware of severity criteria for entry to a trial [ 5 , 6 ]. Other potential sources of apparent placebo responses include sampling biases caused by the withdrawal of the least improved patients in the placebo arm, non-specific beneficial effects resulting from interactions with staff delivering the trial, environmental effects due to inpatient care during placebo-controlled trials, or other unaccounted for factors, such as dietary or exercise changes during the trial [ 7 , 8 , 9 ]. Nonetheless, there is evidence that placebo administration results in ‘true’ - or non-artefactual - placebo effects, that is, identifiable changes in biological systems [ 1 , 10 , 11 ]. For example, placebo administration is capable of causing immunosuppression [ 12 , 13 ], placebo effects in Parkinson’s disease are driven by striatal dopamine release [ 10 , 14 ], and placebo analgesia is mediated by endogenous opioid release [ 15 , 16 ]. Furthermore, there is evidence that placebo effects in depressive and anxiety disorders are correlated with altered activity in the ventral striatum, orbitofrontal cortex, rostral anterior cingulate cortex, and the default mode network [ 17 ]. The placebo effect size can be increased through the use of verbal suggestions and conditioning procedures, thus suggesting the underlying role of psychological mechanisms including learning and expectations [ 11 , 18 ].
Across age groups, treatment modalities, and diverse mental disorders, biological treatments (pharmacotherapy or neurostimulation) do reduce symptoms [ 19 , 20 , 21 , 22 ], but only a subgroup of patients experience a clinically significant symptom response or enter remission [ 23 , 24 , 25 ]. Furthermore, current medications may also have unfavourable side effects [ 23 , 26 , 27 , 28 , 29 , 30 , 31 ]. Given the high prevalence of mental disorders and their significant socioeconomic burden [ 32 , 33 , 34 ], there is a need to develop more effective and safer psychopharmacologic and neurostimulation treatments. However, in randomized-controlled trials (RCTs), the magnitude of the placebo response may be considerable, which can affect the interpretation of their results [ 35 , 36 , 37 ]. For example, in antipsychotic trials over the past 40 years, placebo response has increased while medication response has remained consistent [ 38 , 39 ]. Consequently, the trial’s ability to statistically differentiate between an active medication and a placebo is diminished [ 40 ]. Indeed, large placebo response rates have been implicated in hindering psychotropic drug development [ 41 , 42 ]. The increased placebo response can also affect larger data synthesis approaches, such as network meta-analysis, in which assumptions about placebo responses (e.g. stability over time) might affect the validity of results [ 43 ].
Improved understanding of participant, trial, and mental disorder-related factors that contribute to placebo response might allow better clinical trial design to separate active treatment from placebo effects. There is a growing body of research, including individual studies and systematic reviews/meta-analyses, examining the placebo response within specific mental disorders [ 35 ]. However, to date, no overarching synthesis of this literature, to detect any similarities or differences across mental disorders, has been published. We therefore carried out an umbrella review of meta-analyses to address this need. We aimed to assess the placebo effect size in RCTs for a range of mental disorders, whether the effect size differs across distinct mental disorders, and identify any correlates of increased placebo effect size or response rate.
The protocol for this systematic umbrella review was pre-registered on the open science framework ( https://osf.io/fxvn4/ ) and published [ 44 ]. Deviations from this protocol, and additions to it, were: eight authors were involved in record screening rather than two; we reported effect sizes pooled across age groups and analyses comparing placebo effect sizes between age groups; and we included a meta-analysis that incorporated trials of dietary supplements as well as medications in autism. For the rationale behind these decisions, see eMethods.
Eight authors (NH, AB, VB, LE, OKF, LM, CR, SS) carried out the systematic review and data extraction independently in pairs. Discrepancies were resolved through consensus or through arbitration by a third reviewer (NH or SCo). We searched, without date or language restrictions, up to 23.10.2022, Medline, PsycInfo, EMBASE + EMBASE Classic, and Web of Knowledge for systematic reviews with or without meta-analyses of RCTs of biological treatments (psychopharmacotherapy or neurostimulation) compared with a placebo or sham treatment in individuals with mental disorders diagnosed according to standardized criteria. The full search strategy is included in eMethods. We also sought systematic reviews of RCTs conducted in patients with sleep-wake disorders, since these disorders are included in the DSM-5 and their core symptoms overlap with those of mental disorders [ 45 ]. We retained systematic reviews with or without meta-analyses that reported within-group changes in symptoms in the placebo arm.
Next, to prevent duplication of data, a matrix containing all eligible systematic reviews/meta-analyses for each category of mental disorder was created. Where there were multiple eligible systematic reviews/meta-analyses for the same disorder and treatment, we preferentially included meta-analyses, and if multiple eligible meta-analyses remained, then we included the one containing the largest number of studies for the same disorder and treatment, in line with recent umbrella reviews [ 46 , 47 ].
Data were extracted by at least two among six reviewers (AB, VB, LE, OKF, CR, SS) independently in pairs via a piloted form. All extracted data were further checked by a third reviewer (NH). See eMethods for a list of extracted data.
Our primary outcome was the pre-post effect size of the placebo/sham related to the condition-specific primary symptom change for each mental disorder. Secondary outcomes included any other reported clinical outcomes in eligible reviews. We report effect sizes calculated within-group from baseline and post-treatment means by meta-analysis authors, including Cohen’s d and Hedges’ g for repeated measures, which account for both mean difference and correlation between paired observations; and standardized mean change, where the average change score is divided by standard deviation of the change scores. We interpreted the effect size in line with the suggestion by Cohen [ 48 ], i.e. small (~0.2), medium (~0.5), or large (~0.8).
In addition, we extracted data regarding potential correlates of increased placebo effect size or response rate (as defined and assessed by the authors of each meta-analysis) in each mental disorder identified through correlation analyses or meta-regression. Where available, results from multivariate analyses were preferred.
The methodological quality of included reviews was assessed by at least two among six reviewers (AB, VB, LE, OKF, NH, CR) independently and in pairs using the AMSTAR-2 tool, a critical appraisal tool that enables reproducible assessments of the conduct of systematic reviews [ 49 ]. The methodological quality of each included review was rated as high, moderate, low, or critically low.
Our initial search identified 6,108 records. After screening titles and abstracts, we obtained and assessed 115 full-text reports (see eResults for a list of articles excluded following full-text assessment, with reasons). Of these, 20 were deemed eligible, and all were systematic reviews with meta-analysis (Fig. 1 ). In total, the 20 included meta-analyses synthesized data from 1,691 RCTs (median 55) involving 261,730 patients (median 5,365). These meta-analyses were published between 2007 and 2022 and involved individuals with the following mental disorders: major depressive disorder (MDD; n = 6) [ 50 , 51 , 52 , 53 , 54 , 55 ], anxiety disorders ( n = 4) [ 55 , 56 , 57 , 58 ], schizophrenia spectrum disorders ( n = 3) [ 38 , 59 , 60 ], alcohol use disorder (AUD; n = 1) [ 61 ], attention-deficit/hyperactivity disorder (ADHD; n = 1) [ 62 ], autism spectrum disorders ( n = 1) [ 63 ], bipolar depression ( n = 1) [ 64 ], intellectual disability ( n = 1) [ 65 ], obsessive-compulsive disorder (OCD; n = 1) [ 66 ], primary insomnia ( n = 1) [ 67 ], and restless legs syndrome (RLS; n = 1) [ 68 ].
Twenty meta-analyses were included.
The methodological quality of the included meta-analyses according to AMSTAR-2 ratings was high in two meta-analyses (ADHD and autism), low in four meta-analyses, and critically low in the remaining 14 meta-analyses (Table 1 ). The most common sources of bias that led to downgrading on the AMSTAR-2 were: no list of excluded full-text articles with reasons ( k = 14), no explicit statement that the protocol was pre-registered ( k = 14), and no assessment of the potential impact of risk of bias in individual studies on the results ( k = 13). The full reasoning behind our AMSTAR-2 ratings is included in eResults.
Our first objective was to determine placebo effect sizes across mental conditions. Data regarding within-group placebo efficacy were reported in sixteen of the included meta-analyses [ 38 , 50 , 52 , 53 , 55 , 56 , 57 , 58 , 60 , 61 , 62 , 63 , 65 , 66 , 67 , 68 ]. Placebo effect sizes for the primary outcomes ranged from 0.23 to 1.85, with a median of 0.64 (Fig. 2 ). Median heterogeneity across meta-analyses was I 2 = 72%, suggesting a generally high percentage of heterogeneity due to true variation across studies.
Dots represent placebo group effect size while triangles represent active effect size. CI confidence interval, MDD major depressive disorder, GAD generalized anxiety disorder, SAD social anxiety disorder, OCD obsessive-compulsive disorder, g Hedges’ g, d Cohen’s d, SMC standardized mean change, NR not reported.
A detailed description of each meta-analysis included for this objective is included in eResults. Here, we report a summary of these results in order of the greatest number of RCT’s and meta-analyses included per disorder. In MDD, a large within-group placebo effect was observed ( g = 1.10, 95% CI [1.06, 1.15]), although active medication had an even larger effect size ( g = 1.49, 95% CI [1.44, 1.53]) [ 50 ]. Similarly, in children and adolescents with MDD, placebo effect size was large ( g = 1.57, 95% CI [1.36, 1.78]), as was serotonergic medication effect size ( g = 1.85, 95% CI [1.70, 2.00]) [ 55 ]. In treatment-resistant MDD, the within-group placebo effect size was smaller than in non-treatment-resistant MDD ( g = 0.89, 95% CI [0.81, 0.98]) [ 52 ]. In neuromodulation trials for MDD, the effect size of sham was g = 0.80 (95% CI [0.65, 0.95]) [ 53 ]. In this meta-analysis, the effect size was larger for non-treatment-resistant ( g = 1.28, 95% CI [0.47, 2.97]) compared to treatment-resistant participants (g = 0.50 95% CI [0.03, 0.99]) [ 53 ]. In adults with anxiety disorders, placebo effect sizes varied across disorders, with a medium effect size in panic disorder ( d = 0.57, 95% CI [0.50, 0.64]) [ 56 ] and large effect sizes in generalized anxiety disorder (GAD) ( d = 1.85, 95% CI [1.61, 2.09]) and social anxiety disorder (SAD) ( d = 0.94, 95% CI [0.77, 1.12]) [ 57 ]. Other meta-analyses in children and adolescents and older adults pooled RCTs across anxiety disorders, and found large placebo effect sizes ( g = 1.03, 95% CI [0.84, 1.21] and d = 1.06, 95% CI [0.71, 1.42], respectively) [ 55 , 58 ]. In ADHD, placebo effect size was medium-to-large for clinician-rated outcomes (SMC = 0.75, 95% CI [0.67, 0.83]) [ 62 ]. There was additionally a significant negative relationship between placebo effect size and drug-placebo difference (−0.56, p < 0.01) for self-rated outcomes [ 62 ]. In schizophrenia spectrum disorders, placebo effect size was small-to-medium in antipsychotic RCTs (SMC = 0.33, 95% CI [0.22, 0.44]) [ 38 ] and medium in RCTs focusing specifically on negative symptoms ( d = 0.64, 95% CI [0.46, 0.83]) [ 60 ]. Placebo effect size in RLS was large when measured via rating scales ( g = 1.41, 95% CI [1.25, 1.56]), but small ( g = 0.02 to 0.24) in RCTs using objective outcomes [ 68 ]. In autism, placebo effect sizes were small (SMC ranged 0.23 to 0.36) [ 63 ]. Similarly, placebo effect size was small in OCD ( d = 0.32, 95% CI [0.22, 0.41]), although larger in children and adolescents ( d = 0.45, 95% CI [0.35, 0.56]) compared with adults ( d = 0.27, 95% CI [0.15, 0.38]) [ 66 ]. Placebo effect size was large in AUD ( g = 0.90, 95% CI [0.70, 1.09]) [ 61 ], small in primary insomnia ( g ranged 0.25 to 0.43) [ 67 ], and medium in intellectual disability related to genetic causes ( g = 0.47, 95% CI [0.18, 0.76]) [ 65 ].
Our second objective was to examine the correlates of increased placebo response. We included 14 meta-analyses that reported correlates of placebo effect size or response rate through correlation analysis or meta-regression [ 38 , 51 , 53 , 54 , 56 , 57 , 59 , 60 , 61 , 62 , 63 , 64 , 66 , 68 ]. The key correlates extracted from these studies are summarized in Table 2 .
Several variables were consistently identified across meta-analyses. Increased number of trial sites was a positive correlate of increased placebo response in MDD [ 51 , 54 ], schizophrenia spectrum disorders [ 59 ], and autism spectrum disorders [ 63 ]. Similarly, increased sample size was positively associated with placebo effect size in schizophrenia spectrum disorders [ 59 ], OCD [ 66 ], and panic disorder [ 56 ]. Later publication or study year was associated with greater placebo response in anxiety disorders [ 56 , 57 ], schizophrenia spectrum disorders [ 38 ], AUD [ 61 ], and OCD [ 66 ] but not in MDD [ 51 ], and with reduced placebo response in ADHD [ 62 ]. Younger age was associated with increased placebo responses in schizophrenia spectrum disorders [ 38 , 59 ] and OCD [ 66 ]. Increased baseline illness severity was associated with increased placebo response in schizophrenia spectrum disorders [ 38 ], ADHD [ 62 ], and AUD [ 61 ]. Increased trial or follow-up duration was positively associated with increased placebo response in MDD [ 51 ], but negatively associated with placebo response in schizophrenia spectrum disorders [ 38 , 60 ] and OCD [ 66 ]. Finally, the effect size of active treatment was positively associated with increased placebo response in neurostimulation trials for MDD [ 53 ], bipolar depression [ 64 ], autistic spectrum disorders [ 63 ], and ADHD [ 62 ].
There were also some variables associated with increased placebo response in single disorders only. Flexible dosing, rather than fixed dosing, was associated with increased placebo response in MDD [ 51 ]. Increased illness duration was associated with reduced placebo response in schizophrenia spectrum disorders [ 38 ]. In RCTs for negative symptoms of schizophrenia, a higher number of active treatment arms was associated with increased placebo response [ 60 ]. A number of treatment administrations was a positive correlate of increased placebo response in patients with AUD [ 61 ]. A low risk of bias in selective reporting was associated with increased placebo response in ADHD [ 62 ]. Finally, a low risk of bias in allocation concealment was associated with increased placebo response in autism [ 63 ].
To our knowledge, this is the first overarching synthesis of the literature exploring the placebo response in RCTs of biological treatments across a broad range of mental disorders. We found that placebo responses were present and detectable across mental disorders. Further, the placebo effect size across these disorders varied between small and large (see Fig. 3 ). Additionally, several variables appeared to be associated with increased placebo effect size or response rate across a number of disorders, while others were reported for individual disorders only.
CI confidence interval, MDD major depressive disorder, GAD generalized anxiety disorder, SAD social anxiety disorder, OCD obsessive-compulsive disorder, g Hedges’ g, d Cohen’s d, SMC standardized mean change.
Our umbrella review distinguishes itself from a recent publication on placebo mechanisms across medical conditions [ 69 ]. Only four systematic reviews of research in mental disorders were included in that recent review [ 69 ], none of which were eligible for inclusion in our umbrella review, as we focus specifically on RCTs in mental disorders. Thus, our current umbrella review synthesizes different literature and is complementary [ 69 ].
We found substantial variation in placebo effect sizes across mental disorders. In GAD, SAD, MDD, AUD, and RLS (for subjective outcomes), placebo effects were large (>0.9), while they were small (approximately 0.3) in OCD, primary insomnia, autism, RLS (for objective outcomes), and schizophrenia spectrum disorders. It is noteworthy that placebo effect size/response rate correlated with active treatment effect size/response rate in many disorders (MDD, bipolar depression, ADHD, and autism). Nonetheless, where reported, active treatment was always superior. This possibly suggests an underlying ‘treatment responsiveness’ of these disorders that can vary in size. Perhaps, the natural history of a disorder is an important factor in ‘responsiveness’, i.e., disorders in which there is greater natural fluctuation in severity will show larger placebo (and active treatment) effect sizes. Supporting this hypothesis, increased trial duration predicted a larger placebo effect size in MDD, a disorder in which the natural course includes improvement [ 31 , 51 , 70 ]. Conversely, in schizophrenia spectrum disorders where improvement (particularly of negative symptoms) is less likely [ 71 ], increased trial and illness duration predicted a smaller placebo effect size [ 38 , 60 ]. However, previous meta-analyses suggest that natural improvement, for example, measured via waiting list control, does not fully account for the placebo effect in depression and anxiety disorders [ 72 , 73 ]. Statistical artifact, therefore, does not seem to fully explain the variation in effect size.
Non-specific treatment mechanisms are likely an additional source of the observed placebo effect. For example, those with treatment-resistant illness might have reduced expectations regarding treatment. This assumption is supported by the subgroup analysis reported by Razza and colleagues showing sham neuromodulation efficacy reduced as the number of previous failed antidepressant trials increased [ 53 ]. Another factor to consider is the outcome measure chosen. For example, the placebo effect size in panic disorder was smaller when calculated with objective or self-report measures compared with clinician-rated measures [ 56 ]. A similar finding was reported in ADHD trials [ 62 ]. Why placebo effect sizes would differ with clinician-rated versus self-rated scales is unclear. This might result from ‘demand characteristics’ (i.e., cues that suggest to a patient how they ‘should’ respond), or unblinding of the rater, or a combination of the two [ 74 , 75 ].
Several correlates of increased placebo response were reported in included meta-analyses. These included a larger sample size, more study sites, a later publication year (but with an opposite finding for ADHD), younger age, and increased baseline illness severity. This might reflect changes in clinical trial methods over time, the potential for increased ‘noise’ in the data with larger samples or more study sites, and, more speculatively, variables associated with increased volatility in symptoms [ 39 , 51 , 76 ]. A more extensive discussion regarding the potential reasons these variables might correlate with, or predict, placebo response is included in the eDiscussion. Although some correlates of increased placebo response were identified, perhaps more pertinently, it is unknown whether these also predict the separation between active treatment and placebo in most mental disorders. Three included meta-analyses did show that as placebo response increases, the likelihood of drug-placebo separation decreases [ 38 , 62 , 64 ]. This suggests correlates of placebo effect size are also correlates of trial success or failure, but this hypothesis needs explicit testing. In addition, few of the meta-analyses we included explored whether correlates of placebo response differed from correlates of active treatment response. For example, in clinical trials for gambling disorder, response to active treatment was predicted by weeks spent in the trial and by baseline severity, while response to placebo was predicted by baseline depressive and anxiety symptoms [ 77 ]. Furthermore, there is evidence that industry sponsorship is a specific correlate of reduced drug-placebo separation in schizophrenia spectrum disorders [ 78 ]. The largest meta-analysis that we included (conducted by Scott et al. [ 50 ]) did not explore correlates of increased placebo response through meta-regression analysis; rather, it was designed specifically to assess the impact of the use of placebo run-in periods in antidepressant trials. The authors found that use of a placebo run-in was associated with reduced placebo response. However, this effect did not enhance sensitivity to detect medication efficacy versus control groups, as trials with placebo run-in periods were also associated with a reduced medication response. Similar effects of placebo run-in were seen in univariate (but not multivariable) models in ADHD, where placebo run-in reduced placebo effect size in youth, but did not affect drug vs placebo difference [ 62 ]. Further work should be undertaken to ascertain whether trial-level correlates (including the use of placebo run-in) differentially explain active treatment or placebo response and whether controlling for these can improve drug-placebo separation.
Our results should be considered in the light of several possible limitations. First, as in any umbrella review, we were limited by the quality of the meta-analyses we included. Our AMSTAR-2 ratings suggest that confidence in the conclusions of most included meta-analyses should be critically low or low. Indeed, several meta-analyses did not assess for publication bias or for bias in included RCTs. This is relevant, as the risk of bias in selective reporting was highlighted as potentially being associated with placebo effect size in ADHD [ 62 ], and might therefore be relevant in other mental disorders. Second, our results are potentially vulnerable to biases or unmeasured confounders present in the included meta-analyses. Third, we attempted to prevent overlap and duplication of information by including only the meta-analyses with the most information. This might, however, have resulted in some data not being included in our synthesis. Fourth, an exploration of the potential clinical relevance of the placebo effect sizes reported here was outside the scope of the current review but should be considered an important question for future research. Finally, the meta-analyses we included encompassed RCTs with different levels of blinding (double-blind, single-blind). Although the majority of trials were likely double-blind, it is possible that different levels of blinding could have influenced placebo effect sizes through effects on expectations. Future analyses of placebo effects and their correlates should either focus on double-blind trials or compare results across levels of blinding. Related to this, the included meta-analyses pooled phase 2 and phase 3 trials (the latter of which will usually follow positive phase 2 trials), which might result in different expectation biases. Therefore, placebo effects should be compared between phase 2 and phase 3 trials in the future.
In this umbrella review, we found placebo effect sizes varied substantially across mental disorders. The sources of this variation remain unknown and require further study. Some variables were correlates of increased placebo response across mental disorders, including larger sample size, higher number of study sites, later publication year (opposite for ADHD), younger age, and increased baseline illness severity. There was also evidence that clinician-rated outcomes were associated with larger placebo effect sizes than self-rated or objective outcomes. We additionally identified important gaps in the literature, with no eligible systematic reviews identified in stress-related disorders, eating disorders, behavioural addictions, or bipolar mania. In relation to these disorders, some analyses have been published but they have not been included in systematic reviews/meta-analyses (e.g. analyses of individual patient data pooled across RCTs in acute mania [ 79 ] or gambling disorder [ 77 , 80 ]) and therefore were not eligible for inclusion here. We also focused on placebo response in RCTs of pharmacotherapies and neurostimulation interventions for mental disorders. We did not include placebo effects in psychosocial interventions, but such an analysis would also be valuable. Future studies should address these gaps in the literature and furthermore should compare findings in placebo arms with active treatment arms, both regarding treatment effect size and its correlates. Gaining additional insights into the placebo response may improve our ability to separate active treatment effects from placebo effects, thus paving the way for potentially effective new treatments for mental disorders.
The datasets generated during and/or analysed during the current study are available in the Open Science Framework repository, https://osf.io/fxvn4/ .
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Dr Nathan TM Huneke is an NIHR Academic Clinical Lecturer. The views expressed in this publication are those of the author(s) and not necessarily those of the NIHR, NHS, or the UK Department of Health and Social Care. For the purpose of open access, the author has applied a Creative Commons Attribution License (CC BY) to any Author Accepted Manuscript version arising from this submission.
NTMH, JA, DSB, SRC, CUC, MG, CMH, RH, ODH, JMAS, MS, and SCo conceptualized the study. NTMH, AB, VB, LE, CJG, OKF, LM, CR, SS, and SCo contributed to data collection, data curation, or data analysis. NTMH, MS, and SCo wrote the first draft of the manuscript. All authors had access to the raw data. All authors reviewed and edited the manuscript and had final responsibility for the decision to submit it for publication.
These authors contributed equally: Marco Solmi, Samuele Cortese.
Clinical and Experimental Sciences, Faculty of Medicine, University of Southampton, Southampton, UK
Nathan T. M. Huneke, Jay Amin, David S. Baldwin, Samuel R. Chamberlain, Matthew Garner, Catherine M. Hill, Ruihua Hou, Konstantinos Ioannidis, Julia M. A. Sinclair & Samuele Cortese
Southern Health NHS Foundation Trust, Southampton, UK
Nathan T. M. Huneke, Jay Amin, David S. Baldwin, Samuel R. Chamberlain, Konstantinos Ioannidis & Satneet Singh
University Department of Psychiatry and Mental Health, University of Cape Town, Cape Town, South Africa
David S. Baldwin
School of Psychology, University of Nottingham Malaysia, Semenyih, Malaysia
Alessio Bellato
Centre for Innovation in Mental Health, School of Psychology, Faculty of Environmental and Life Sciences, University of Southampton, Southampton, UK
Alessio Bellato, Valerie Brandt, Matthew Garner, Corentin J. Gosling, Claire Reed, Marco Solmi & Samuele Cortese
Clinic of Psychiatry, Social Psychiatry and Psychotherapy, Hannover Medical School, Hanover, Germany
Valerie Brandt
Department of Child and Adolescent Psychiatry, Charité Universitätsmedizin Berlin, Berlin, Germany
Christoph U. Correll
Department of Psychiatry, Zucker Hillside Hospital, Northwell Health, Glen Oaks, NY, USA
Department of Psychiatry and Molecular Medicine, Zucker School of Medicine at Hofstra/Northwell, Hempstead, NY, USA
Center for Psychiatric Neuroscience, Feinstein Institute for Medical Research, Manhasset, NY, USA
Faculty of Education and Psychology, University of Navarra, Pamplona, Spain
Luis Eudave
School of Psychology, Faculty of Environmental and Life Sciences, University of Southampton, Southampton, UK
Matthew Garner
Université Paris Nanterre, DysCo Lab, F-92000, Nanterre, France
Corentin J. Gosling
Université de Paris, Laboratoire de Psychopathologie et Processus de Santé, F-92100, Boulogne-Billancourt, France
Department of Sleep Medicine, Southampton Children’s Hospital, Southampton, UK
Catherine M. Hill
Department of Psychosis Studies, Institute of Psychiatry, Psychology & Neuroscience, King’s College London, London, UK
Oliver D. Howes
H Lundbeck A/s, Iveco House, Watford, UK
Institute of Clinical Sciences (ICS), Faculty of Medicine, Imperial College London, London, UK
Department of Clinical Medicine, Aarhus University, Aarhus, Denmark
Ole Köhler-Forsberg
Psychosis Research Unit, Aarhus University Hospital–Psychiatry, Aarhus, Denmark
Department of Translational Biomedicine and Neuroscience (DIBRAIN), University of Studies of Bari “Aldo Moro”, Bari, Italy
Lucia Marzulli
Department of Psychiatry, University of Ottawa, Ottawa, ON, Canada
Marco Solmi
Department of Mental Health, Ottawa Hospital, Ottawa, ON, Canada
Ottawa Hospital Research Institute (OHRI) Clinical Epidemiology Program, University of Ottawa, Ottawa, ON, Canada
School of Epidemiology and Public Health, Faculty of Medicine, University of Ottawa, Ottawa, ON, Canada
Solent NHS Trust, Southampton, UK
Samuele Cortese
DiMePRe-J-Department of Precision and Regenerative Medicine-Jonic Area, University “Aldo Moro”, Bari, Italy
Hassenfeld Children’s Hospital at NYU Langone, New York University Child Study Center, New York, NY, USA
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Correspondence to Nathan T. M. Huneke .
Competing interests.
DSB is President of the British Association for Psychopharmacology, Editor of the Human Psychopharmacology journal (for which he receives an editor’s honorarium), and has received royalties from UpToDate. CMH has acted on an expert advisory board for Neurim Pharmaceuticals. ODH is a part-time employee and stockholder of Lundbeck A/s. He has received investigator-initiated research funding from and/or participated in advisory/speaker meetings organized by Angellini, Autifony, Biogen, Boehringer-Ingelheim, Eli Lilly, Heptares, Global Medical Education, Invicro, Jansenn, Lundbeck, Neurocrine, Otsuka, Sunovion, Recordati, Roche and Viatris/Mylan. ODH has a patent for the use of dopaminergic imaging. All other authors declare no competing interests. MS has received honoraria/has been a consultant for Angelini, Lundbeck, and Otsuka. SCo has received honoraria from non-profit associations (BAP, ACAMH, CADDRA) for educational activities and an honorarium from Medice. KI has received honoraria from Elsevier for editorial work. SRC receives honoraria from Elsevier for associate editor roles at comprehensive psychiatry and NBR journals. CUC has been a consultant and/or advisor to or has received honoraria from: AbbVie, Acadia, Adock Ingram, Alkermes, Allergan, Angelini, Aristo, Biogen, Boehringer-Ingelheim, Bristol-Meyers Squibb, Cardio Diagnostics, Cerevel, CNX Therapeutics, Compass Pathways, Darnitsa, Denovo, Gedeon Richter, Hikma, Holmusk, IntraCellular Therapies, Jamjoom Pharma, Janssen/J&J, Karuna, LB Pharma, Lundbeck, MedAvante-ProPhase, MedInCell, Merck, Mindpax, Mitsubishi Tanabe Pharma, Mylan, Neurocrine, Neurelis, Newron, Noven, Novo Nordisk, Otsuka, Pharmabrain, PPD Biotech, Recordati, Relmada, Reviva, Rovi, Sage, Seqirus, SK Life Science, Sumitomo Pharma America, Sunovion, Sun Pharma, Supernus, Takeda, Teva, Tolmar, Vertex, and Viatris. He provided expert testimony for Janssen and Otsuka. He served on a Data Safety Monitoring Board for Compass Pathways, Denovo, Lundbeck, Relmada, Reviva, Rovi, Supernus, and Teva. He has received grant support from Janssen and Takeda. He received royalties from UpToDate and is also a stock option holder of Cardio Diagnostics, Kuleon Biosciences, LB Pharma, Mindpax, and Quantic.
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PLACEBO EFFECTS IN RANDOMIZED TRIALS OF PHARMACOLOGICAL AND NEUROSTIMULATION INTERVENTIONS FOR MENTAL DISORDERS: AN UMBRELLA REVIEW SUPPLEMENTARY APPENDIX
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Huneke, N.T.M., Amin, J., Baldwin, D.S. et al. Placebo effects in randomized trials of pharmacological and neurostimulation interventions for mental disorders: An umbrella review. Mol Psychiatry (2024). https://doi.org/10.1038/s41380-024-02638-x
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DOI : https://doi.org/10.1038/s41380-024-02638-x
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Anne m. verhallen.
University of Groningen, University Medical Center Groningen, Department of Biomedical Sciences of Cells & Systems, Cognitive Neuroscience Center, Groningen, the Netherlands
Jan-bernard c. marsman, gert j. ter horst, associated data.
The data will not be stored at a public repository due to restrictions from the informed consent (subjects have not given consent to have their data publicly stored) and European data privacy regulations (GDPR). The data are available on request. A data access committee has been put in place, consisting of Prof G.J. ter Horst (Principal Investigator of the study), J.B.C. Marsman and Prof A. Aleman (head of the Cognitive Neuroscience Center), who will review requests and assure accessibility of the data. This access committee can be reached via [email protected] .
The occurrence of a stressful event is considered to increase the risk of developing depression. In the present study we explore whether the breakup of a romantic relationship can be used as an experimental model to study a depression-like state during a period of stress in individuals without a psychiatric disorder. The primary aim of our study was to investigate: 1) whether individuals with a recent romantic relationship breakup (‘‘heartbreak”) demonstrate symptoms of depression, 2) how to describe heartbreak characteristics based on data from a comprehensive questionnaire battery, and 3) whether this description can capture severity of depression symptoms. Secondary, we were interested in gender differences with regard to the above study objectives. Subjects who have experienced a relationship breakup in the preceding six months ( N = 71) or are in a romantic relationship ( N = 46) participated in our study. A questionnaire battery was administered to acquire information related to depression, mood, the breakup and (former) relationship. Principal Component Analysis with Procrustes bootstrapping was performed to extract components from the questionnaire data. Even though our sample of individuals who recently have experienced a relationship breakup can be on average considered non-depressed, group-level depression scores were elevated compared to individuals in a relationship ( p = .001) and 26.8% reported symptoms corresponding to mild, moderate or severe depression. We described heartbreak by two principal components interpreted as ‘‘sudden loss” and ‘‘lack of positive affect”, respectively. Highly significant correlations between the component scores and depression scores were found ( p < .001 and p < .001, respectively), although these correlations differed between the genders. Based on these findings, we propose that the experience of a romantic relationship breakup is a viable experimental model to examine symptoms of depression in individuals without a psychiatric disorder. This way, stress-related coping and depression vulnerability can be studied in further research.
Stressful life-events are considered to be risk factors for the development of depression[ 1 ]. Kendler et al.[ 2 ] investigated the interplay between stressful events, genetic predisposition and depression among female twins and found that both heredity and occurrence of stressful events contributed to the onset of depressive episodes independently. Especially events with a high impact, such as death of a close family member and divorce, elevated the probability of developing a depressive episode[ 2 ], although the majority of people do not develop a depressive episode following the experience of an upsetting event. Hence, research focusing on stressful and emotionally upsetting events can give valuable insights into individual differences regarding stress-related coping and the link between stress and depression.
In this study we set out to investigate mood and depression symptoms during a period of stress in a population without a psychiatric disorder. More precisely, we explore whether the breakup of a romantic relationship can be used as an experimental model to study a depression-like state. Previous research already showed that the breakup of a romantic relationship can be seen as an emotionally upsetting event that can lead to multiple symptoms related to sadness, grief and depression and even can result in an increased risk of developing a depressive episode[ 3 – 6 ]. In a university student sample, severe breakup distress, measured with a questionnaire concerning symptoms of grief, was accompanied by feelings of betray and rejection, depression symptoms, anxiety symptoms, intrusive thoughts about the ex-partner and sleep disturbances[ 3 ]. The elapsed time since the breakup, self-reported quality of the former relationship, feelings of betray and depression scores especially predicted the severity of breakup distress[ 3 ]. Additionally, women reported higher breakup distress scores compared to men in that study[ 3 ]. In a study of Stoessel et al.[ 4 ], all of the subjects with a relationship breakup in the preceding six months and experiencing feelings of sadness about the breakup reported symptoms corresponding to clinical depression. In women with a breakup in the preceding four months, high levels of complicated grief (extreme symptoms of grief interfering with daily life functioning) were present in four of the eight subjects. In addition, a different brain pattern (increased activity in posterior regions such as the cerebellum and decreased activity in anterior regions such as the insula and temporal cortex) was found in these women when ruminating about their ex-partner in comparison with thinking about an acquaintance in a neutral manner[ 5 ]. Moreover, epidemiological data indicated an association between the occurrence of a romantic relationship breakup and first onset of major depression in a young population[ 6 ].
As it is known that the prevalence of depression is higher in women, we were also interested in differences in depression (-like) symptoms between the genders in our study. For example, data from a United States survey revealed a 1.7 times higher lifetime prevalence of depressive episodes among women[ 7 ]. Differences in stress sensitivity between the genders could play a role, as stress paradigms in rodents elucidated different stress responses between males and females[ 8 , 9 ]. Moreover, gender differences with regard to rumination might be involved. It is known that women tend to ruminate more during periods of stress[ 10 ]. A ruminative coping strategy was associated with both anxiety and depression symptoms and correlated significantly with occurrence of new depressive episodes in patients with major depressive disorder[ 11 ]. In addition, experiencing ruminating thoughts about the loss during grief was found to be related to maladaptive grieving and the development of symptoms of depression[ 12 ].
In the present study, we primarily aimed to investigate: 1) whether individuals with a recent romantic relationship breakup (‘‘heartbreak”) demonstrate symptoms of depression, 2) how to describe heartbreak characteristics based on data from a comprehensive questionnaire battery, and 3) whether this description can capture severity of depression symptoms. Secondary, we were interested in gender differences with regard to the above study objectives. To this end, young men and women, either with a recent romantic relationship breakup (the ‘‘heartbreak group”) or in a romantic relationship (the ‘‘relationship group”) participated. The relationship group was included in the study as a reference group with absence of stress resulting from a romantic relationship breakup. We expected a higher severity of depression symptoms in the heartbreak group compared to the relationship group. Given that women are more at risk for developing depression in the general population, we expected a higher severity of depression symptoms among the women in the heartbreak group than the men in the heartbreak group.
Experimental design.
Subjects were invited to our laboratory to participate in the study between 2011 and 2013. The experiment comprised a self-report questionnaire battery and fMRI paradigm with a cross-sectional design. fMRI results will be reported elsewhere. Before the start of the study, written informed consent was obtained from every subject. Study procedures were approved by the Medical Ethical Committee of the University Medical Center Groningen and conducted in accordance with the principles of the Declaration of Helsinki. Subjects received a financial compensation for their participation.
Subjects were recruited by distributing posters around faculty buildings of the University of Groningen and promoting the study using (social) media. Women of the heartbreak group (‘‘heartbroken females”) were recruited using recruitment material with terminology implying that subjects have to suffer from breakup distress to participate. With this recruitment strategy it was not possible to include a sufficient number of male subjects. Therefore, a subsample of the men of the heartbreak group (‘‘heartbroken males”) was recruited using recruitment material referring to the experience of a relationship breakup instead of suffering from breakup distress. Potential subjects could send an email to show their interest in the study and exchange contact information. A telephone intake interview was planned to explain study procedures and check inclusion and exclusion criteria. Additionally, subjects received written information. During the first stage of the study, heartbroken females were pre-selected at the intake interview based on their self-report level of sadness about the breakup on a scale from 1 to 10, because at that time we intended to compare women with contrasting levels of breakup distress. For the results presented in this paper we did not divide the heartbreak group in subgroups based on information obtained at the intake interview.
For both the heartbreak group and the relationship group, subjects had to be between the age of 18 and 26 years, right-handed, Western, heterosexual and Dutch speaking. Female subjects could only participate if they used hormonal contraception and were in the continuation phase on the day of the experiment to minimize possible effects of fluctuating sex hormone levels on our outcome measures. To participate in the heartbreak group, subjects had to have a relationship breakup within the preceding six months and a relationship duration of at least six months. To participate in the relationship group, subjects had to have a relationship duration between 6 and 24 months because we intended to include subjects whose relationship has not yet evolved into a companionate stage[ 13 ]. Subjects with a relationship duration shorter than 6 months were excluded due to previous research on increased stress hormone level during these first periods[ 14 ]. For both the heartbreak group and the relationship group, subjects with neurological abnormalities, MRI contraindications such as ferromagnetic metal parts in the body, (suspected) pregnancy and claustrophobia, use of psychotropic medication in the last five years, alcohol and/or drug abuse and physical and/or sexual abuse during the relationship (all self-reported) were not allowed to participate in the study. 71 and 46 subjects were included in the heartbreak group and the relationship group, respectively. After the fMRI scanning session, one subject from the heartbreak group was excluded because of substantial brain ventricle abnormalities.
A self-report questionnaire battery in Dutch was administered to assess psychological and behavioral information of the subjects. Before filling in the questionnaire battery, background information, such as highest completed educational level according to the Dutch educational system and current occupation status, was acquired from the subjects. The heartbreak questionnaire battery consisted of the Major Depression Inventory (MDI) and adjusted versions of the Inventory of Complicated Grief (ICG), Positive and Negative Affect Schedule (PANAS), Perceived Relationship Quality Components Inventory (PRQC), the Hurt-Proneness Scale and the Passionate Love Scale (PLS)[ 13 , 15 – 19 ]. Additionally, in-house designed questions about the breakup were added to the questionnaire battery, covering aspects such as unexpectedness of the breakup and ruminating thoughts about the ex-partner. For each questionnaire, except the in-house designed questionnaire about the breakup, total scores were calculated and used in further analyses. Cronbach’s alpha scores were calculated for each questionnaire (can be found in S1 Table ). The MDI is a 10-item questionnaire to assess symptoms of depression (both core symptoms such as anhedonia and accompanying symptoms such as sleeping difficulties), based on the DSM-IV and ICD-10 diagnostic criteria[ 15 , 20 ]. MDI scores were calculated according to the scoring guidelines for the use of the MDI as a rating scale to measure severity of depression symptoms[ 20 ]. MDI scores theoretically range between 0 and 50. Scores between 0 and 20 indicate absence of clinical depression, scores between 21 and 25 correspond to mild depression, scores between 26 and 30 and scores above 31 indicate respectively moderate and severe depression[ 20 ]. The ICG is used to assess maladaptive grieving after the loss of a loved one[ 16 ]. Similar to the study of Najib et al.[ 5 ], the ICG was adjusted so that it was suitable for heartbreak. Thirteen items were extracted from the original 19-item version, by removing items only applicable to death. ICG scores were calculated by summing the scores of the 13 questions and theoretically range between 13 and 130. The PANAS comprises questions about positive and negative affect, representing current mood[ 17 ]. PANAS scores were calculated for both the positive affect and negative affect part by summing the scores of the 10 questions and theoretically range between 10 and 100[ 17 ]. The PRQC was used to assess self-reported former relationship quality[ 18 ]. In this study a 9-item version of the PRQC was extracted from the original 18-item version. PRQC scores were calculated by summing the scores of the 9 questions and theoretically range between 9 and 90. To what extent the subjects were prone to experience hurt feelings was measured with the Hurt-Proneness Scale[ 19 ]. Hurt proneness scores were calculated by summing the scores of the 6 questions and theoretically range between 6 and 60. Questions 3, 4 and 6 were reversed scored because high scores characterize low hurt proneness. The PLS can be used to assess intensity of romantic love[ 13 ]. A 28-item version of the PLS was extracted from the original 30-item version, by removing two items that are not appropriate for heartbreak. The PLS was filled in exclusively by the subjects who reported to be still in love with their ex-partner at the time of the testing day. PLS scores were not analyzed further. As the PLS was only filled in by the heartbroken subjects who reported to be still in love with their ex-partner, the sample size turned out to be insufficient. All questionnaires, except the MDI, were scored on a 10-point Likert scale, ranging from 1 (‘‘not at all”) to 10 (‘‘extremely”). The MDI was rated on a 6-point Likert scale, ranging from 1 (‘‘not at all”) to 6 (‘‘all the time”). Questions about the relationship breakup were categorical or measured on a 10-point Likert scale. The questionnaire battery of the relationship group consisted of the MDI and adjusted versions of the PANAS, PRQC, Hurt-proneness scale and PLS, similar to the heartbreak group.
Statistical analyses were conducted with IBM SPSS Statistics version 24 for Windows. A Shapiro-Wilk test for normality was used to check if our data were normally distributed. When data distribution was found to be skewed, non-parametric statistical tests were conducted in further analysis steps.
Background information and questionnaire data were compared between the heartbreak group and the relationship group using a Mann-Whitney U test. Concerning the questionnaire battery of the relationship group, only MDI scores are considered in this manuscript, since we aimed to compare severity of depression symptoms between the heartbreak group and the relationship group.
An exploratory Principal Component Analysis (PCA) followed by varimax rotation was performed to extract components representing heartbreak in a data-driven manner. We intended to focus on subjective measures. Consequently, 19 variables were entered into the analysis; ‘‘unexpectedness breakup”, ‘‘feeling rejected”, ‘‘feeling betrayed”, ‘‘feeling angry”, ‘‘feeling sad”, ‘‘feeling disappointed”, ‘‘feeling independent”, ‘‘feeling alone”, ‘‘feeling relieved”, ‘‘feeling hopeful”, ‘‘ruminating thoughts”, ‘‘intrusive thoughts”, ‘‘affection for ex-partner”, ‘‘in love with ex-partner”, ‘‘ICG”, ‘‘PANAS positive”, ‘‘PANAS negative”, ‘‘PRQC” and ‘‘Hurt proneness”. Subjects with missing data were deleted listwise, resulting in a sample size of 69 for the PCA. Principal components were extracted using the correlation matrix, and rotated with varimax with Kaiser normalization[ 21 ]. Parallel analysis was performed to determine the optimal number of components[ 22 ]. We adapted the online available SPSS script for parallel analysis, written by Brian O’Connor, to our dataset ( https://people.ok.ubc.ca/brioconn/nfactors/nfactors.html ) [ 23 ]. Thousand sets of normally distributed data were randomly generated. For each component an eigenvalue belonging to the original data and an eigenvalue belonging to the 95% confidence interval (CI) of the generated data was computed. Components with an eigenvalue greater than the corresponding eigenvalue derived from random normal data generation were considered as ‘‘components”. Subsequently, a PCA followed by a varimax rotation was performed with a fixed number of components to extract, based on the results of the parallel analysis. The outcome of this combined PCA and varimax rotation, a component matrix, was used in the subsequent analyses.
A Procrustes bootstrapping PCA was performed to select the component loadings to be interpreted further. Thousand samples of component matrices were generated by resampling with replacement. To this end, we adjusted the online available SPSS script for component analysis with Procrustes bootstrapping from Linda Reichwein Zientek and Bruce Thompson[ 24 ]. Note that, just like the original PCA-varimax, components were not normalized row wise. Bootstrapping results were rotated towards a target matrix. The target matrix was constructed by binarizing the component matrix retaining the sign. Variables were assigned 1 or -1 for the component they loaded strongest on and 0 elsewhere. 95% CIs were calculated for each variable across the thousand bootstrap resamples.
Only variables with a 95% CI that does not cross zero were interpreted further. Labels were assigned to each component based on the component loadings acquired with the original PCA-varimax.
For each subject, component scores were computed using regression. A Spearman rank test was conducted to see how well the component scores correlate with MDI scores. A Spearman rank test was used to assess the correlation between the component scores, time since breakup and relationship duration. Component scores were compared between men and women with an independent samples t-test. Additionally, Spearman rank correlations between the component scores and MDI scores were calculated for men and women separately.
For all conducted statistical tests, results were considered significant at p -value < .05 (uncorrected), two-tailed.
The relationship group consisted of 23 men and 23 women with a relationship duration between 6 and 24 months ( Mdn = 13.00, IQR = 9.00–19.00). Age ranged between 18 and 26 years ( Mdn = 21.00, IQR = 20.00–23.00). The heartbreak group consisted of 33 men and 38 women. Age ranged between 18 and 25 years ( Mdn = 22.00, IQR = 21.00–24.00). Relationship duration prior to the breakup ranged between 6 and 81 months ( Mdn = 20.00, IQR = 13.00–37.00). Time since breakup ranged between 0 and 5 months ( Mdn = 2.00, IQR = 1.00–4.00). In 42.3% of the subjects, the ex-partner decided to break up, whereas in 35.2% the breakup was initiated by the subject and in 22.5% the subject and ex-partner decided together. 70.4% of the subjects reported to still be in touch with their ex-partner. Five subjects (7.0%) reported to have found a new romantic partner. 70.4% reported to still think about their ex-partner on a daily basis and 25.4% experienced physical complaints after the breakup. The heartbreak group was significantly older than the relationship group ( U = 1241.00, Z = -2.21, p = .027, r = -.20). Additional background information of our study population can be found in S2 Table .
Fig 1 shows the severity of depression symptoms for the relationship group and the heartbreak group. MDI total scores ranged between 2 and 22 ( Mdn = 7.00, IQR = 4.75–10.25) in the relationship group. 97.8% were found to have a MDI score below 21, corresponding to an absence of depression. 2.2% had depression symptoms corresponding to mild depression. MDI scores ranged between 1 and 45 ( Mdn = 9.00, IQR = 7.00–21.00) in the heartbreak group. 12.7% reported depression symptoms corresponding to mild depression. 1.4% and 12.7% reported symptoms corresponding to respectively moderate and severe depression. In total, 26.8% reported symptoms corresponding to mild, moderate or severe depression. MDI total scores were higher in the heartbreak group compared to the relationship group ( U = 1042.00, Z = -3.31, p = .001, r = -.31). No gender differences were found ( U = 213.50, Z = -1.13, p = .260, r = -.17) between the males ( Mdn = 6.00, IQR = 4.00–8.00) and females ( Mdn = 7.00, IQR = 5.00–14.00) in the relationship group. MDI scores differed ( U = 380.00, Z = -2.85, p = .004, r = -.34) between heartbroken males ( Mdn = 7.00, IQR = 4.50–14.00) and heartbroken females ( Mdn = 15.50, IQR = 7.75–25.00). S3 Table shows the median and interquartile range for the individual items for the two groups. With regard to the core symptoms of depression, the heartbreak group scored higher on the item ‘‘feeling sad or low in spirits” and the item ‘‘loss of interest in daily activities” ( p = .001 and p = .013), while the item ‘‘lack of energy and strength” did not differ between the two groups ( p = .218). Concerning the accompanying symptoms of depression, the items ‘‘feeling less self-confident”, ‘‘the feeling that life was not worth living”, ‘‘concentration difficulties”, ‘‘feeling restless/listless” and ‘‘sleeping difficulties” differed significantly between the two groups (all higher in the heartbreak group, p = .019, p = .002, p = .019, p < .001, and p = .004, respectively). No differences were found regarding the items ‘‘feelings of guilt” and ‘‘decreased/increased appetite” ( p = .112 and p = .151).
Outliers (values that are between Q1-1.5*IQR or Q3+1.5*IQR and Q1-3*IQR or Q3+3*IQR) are indicated with a circle. Extreme outliers (values that are beyond Q1-3*IQR or Q3+3*IQR) are indicated with a star.
To characterize the heartbreak group, a PCA-varimax was performed on the questionnaire battery. Subsequently, the relation with the depression scores was investigated.
Parallel analysis revealed two components with corresponding eigenvalues greater than the concomitant eigenvalue calculated for a random dataset, explaining respectively 45.8% and 13.8% of the variance.
Table 1 shows the component loadings for the included variables for the two components. Additionally, the 95% CIs of the component loadings are shown. Given that the variables ‘‘feeling betrayed”, ‘‘feeling rejected”, ‘‘feeling angry”, ‘‘unexpectedness breakup” and ‘‘ICG” load highly on component 1 (95% CI does not straddle zero), this component was interpreted as ‘‘sudden loss”. The variables ‘‘feeling hopeful” and ‘‘PANAS positive” load strongest (inversely) on component 2 and have 95% CIs that do not contain zero. Therefore, this component was interpreted as ‘‘lack of positive affect”.
Component 1 | Component 2 | |
---|---|---|
1. Unexpectedness breakup | .78 [.67, .87] | -.13 [-.27, .15] |
2. Feeling rejected | .88 [.79, .92] | .12 [.03, .36] |
3. Feeling betrayed | .89 [.81, .93] | -.11 [-.19, .15] |
4. Feeling angry | .84 [.69, .92] | -.01 [-.11, .24] |
5. Feeling relieved | -.47 [-.61, -.23] | -.57 [-.74, -.42] |
6. Feeling sad | .67 [.48, .76] | .51 [.42, .69] |
7. Feeling disappointed | .73 [.56, .81] | .40 [.28, .64] |
8. Feeling independent | .04 [-.20, .34] | -.57 [-.72, -.35] |
9. Feeling alone | .48 [.25, .60] | .62 [.46, .80] |
10. Feeling hopeful | -.10 [-.22, .13] | -.83 [-.89, -.73] |
11. Ruminating thoughts | .57 [.38, .65] | .70 [.63, .82] |
12. Intrusive thoughts | .52 [.30, .62] | .58 [.45, .75] |
13. In love with ex-partner | .50 [.24, .65] | .50 [.33, .72] |
14. Affection for ex-partner | .02 [-.29, .30] | .60 [.37, .75] |
15. ICG | .78 [.63, .83] | .49 [.43, .66] |
16. PANAS positive | .10 [-.05, .34] | -.76 [-.85, -.57] |
17. PANAS negative | .61 [.38, .75] | .42 [.26, .66] |
18. PRQC | .62 [.38, .74] | .25 [.06, .55] |
19. Hurt proneness | .13 [-.17, .44] | .26 [-.11, .56] |
No significant correlation between time since breakup and each of the two components was found (‘‘sudden loss”: r s = .06, p = .600, “lack of positive affect”: r s = -.22, p = .071). Relationship duration correlated significantly with the ‘‘lack of positive affect” component ( r s = .25, p = .039) and did not correlate significantly with the ‘‘sudden loss” component ( r s = -.07, p = .559).
Positive correlations between the component scores belonging to the two extracted components and depression scores were prevalent ( r s = .57, p < .001 and r s = .49, p < .001 for the ‘‘sudden loss” component and the ‘‘lack of positive affect” component, respectively). The scatterplot between the ‘‘sudden loss” component and MDI and between the ‘‘lack of positive affect” component and MDI are shown in Fig 2A and Fig 2B , respectively.
(A) Relationship between the ‘‘sudden loss” component and MDI. (B) Relationship between the ‘‘lack of positive affect” component and MDI.
Gender differences with regard to the ‘‘lack of positive affect” component were found: heartbroken females had higher component scores ( t (67) = 2.95, p = .004, r = .34). Component scores belonging to the ‘‘sudden loss” component did not differ between the genders ( t (67) = .88, p = .385, r = .11). MDI scores correlated positively with both components (see above). However, the MDI score showed a gender effect as well (see above). Therefore, correlations between MDI scores and each of the two components were examined for men and women separately. For heartbroken females, highly significant correlations were found for both ‘‘sudden loss” and ‘‘lack of positive affect” ( r s = .57, p < .001 and r s = .70, p < .001 respectively). Heartbroken males showed a partially different result: a significant correlation between MDI scores and the ‘‘sudden loss” component was prevalent ( r s = .55, p = .001). In contrast, the ‘‘lack of positive affect” component did not correlate significantly with MDI scores ( r s = -.01, p = .951).
In the present study, we primarily aimed to investigate: 1) whether individuals with a recent romantic relationship breakup demonstrate symptoms of depression, 2) how to describe heartbreak characteristics based on data from a comprehensive questionnaire battery, and 3) whether this description can capture severity of depression symptoms. Secondary, we were interested in gender differences with regard to the above study objectives.
In accordance with our expectations, severity of depression symptoms was found to be higher in the heartbreak group compared to the reference group, i.e. subjects in a romantic relationship. MDI total scores as well as individual items, including core symptoms of depression, were elevated. However, median MDI scores of the heartbreak group fell within the range of absence of depression as defined by Bech et al.[ 20 ]. Nonetheless, 26.8% and 14.1% of the heartbroken subjects reported severity of depression symptoms corresponding to respectively mild to severe depression and moderate to severe depression. In contrast, only one subject reported symptoms corresponding to (mild) depression in the relationship group. In a study by Forsell et al.[ 25 ], a mean MDI score of 8.8 (95% CI 8.6–9.0) was found in a large sample of men and women drawn from the general population. Note that even in this general population, 8.0% reported symptoms corresponding to moderate or severe depression[ 25 ] (compared to the 14.1% found in this study). Thus, we consider the heartbreak group as a good population to study a depression-like state in otherwise healthy individuals.
We described heartbreak by two principal components. Feelings of betray, rejection and anger, unexpectedness of the breakup and symptoms of complicated grief contributed substantially to the first component that was therefore interpreted as ‘‘sudden loss”. Feeling hopeful after the breakup and current positive affect (i.e. the ability to experience positive emotions) contributed largely (inversely) to the second component that was consequently interpreted as ‘‘lack of positive affect”. The finding that the feeling of being betrayed is an important parameter of heartbreak is consistent with the study of Field et al.[ 3 ]. Moreover, our findings show similarities with a retrospective study concerning emotions following a relationship dissolution by Barbara and Dion[ 26 ]. In that study, a component labeled as ‘‘negative emotions” was extracted and rejection and anger were found to be important variables for that specific component[ 26 ]. This is in accordance with the high loadings of the variables ‘‘feeling rejected” and ‘‘feeling angry” on the ‘‘sudden loss” component as found in our study.
Within the heartbreak group, both components correlated highly with depression scores. The ‘‘lack of positive affect” component is primarily defined by positive affect scores, as measured with the PANAS. This is in accordance with a study by Crawford and Henry[ 27 ] in which positive affect was found to be specifically related to depression scores in a large sample of men and women drawn from the general population. The ‘‘sudden loss” component also correlated highly with depression scores. This is consistent with literature regarding grief. For example, Keyes et al.[ 28 ] found associations between the experience of an unexpected death of a loved one and prevalence of psychiatric problems including clinical depression.
As expected, heartbroken females reported higher depression scores than heartbroken males in our study. This cannot be explained by general gender differences, given that the depression scores of the men and women of the relationship group did not differ, and therefore seems to be breakup-related. Among the heartbroken males examined separately, no association between the ‘‘lack of positive affect” component and severity of depression symptoms was found. Additionally, women had higher scores on the ‘‘lack of positive affect” component than men. Tentatively, these findings suggest that men are less likely to demonstrate and/or report reduced abilities experiencing positive emotions during a period of stress than women and this possibly relates to the well-known differential depression rates among the genders.
By conducting the present study, detailed knowledge about behavioral and psychological consequences of a recent romantic relationship breakup and its association with symptoms of depression was acquired. A potential weakness of our study is that differences in recruitment strategy and pre-selection prior to inclusion between the genders could have influenced our findings. This makes it difficult to draw strong conclusions about effects of gender. Nevertheless, gender-specific application rates can be considered a finding as well in our opinion. Another possible weakness is that already having a new romantic partner was not an exclusion criterion in our study and in our sample five of the 71 subjects reported to have found a new partner on the day of the experiment. One could argue that this will reduce sadness and mood problems associated with a breakup. However, excluding those subjects from our dataset did not change either group-level differences regarding depression scores or the strength of the correlation between the components and depression scores noticeably (data can be found in S1 Appendix ). Therefore, possible effects of having a new romantic partner on our results were considered minimal. Perhaps, finding a new partner cannot diminish breakup-related effects within this limited period of time.
In the present study, we investigated whether the breakup of a romantic relationship can be used as an experimental model to study a depression-like state. We demonstrated an increased range of depression scores among our sample of individuals who recently have experienced a relationship breakup. Furthermore, our results show that the effects of experiencing a relationship breakup can be captured with two descriptors: “sudden loss” and “lack of positive affect”. Both were associated with (severity of) depression (-like) symptoms. Nota bene, this association was gender-dependent. Therefore, we propose that this life-event is a viable experimental model to investigate symptoms of depression in individuals without a psychiatric disorder. This paves the way to investigate the involvement of stress in the transition from healthy-to depressive behavior. Consequently, further longitudinal research using this model could provide new insights into individual-specific coping and vulnerability factors contributing to the development of depression symptoms during a period of stress.
Values are shown as percentage or median (Q1-Q3) for respectively categorical variables and numerical variables.
Values are shown as median (Q1-Q3).
Acknowledgments.
The authors would like to thank the undergraduate students who contributed to the design of the study, recruitment of subjects and data collection (Els van der Meijden, Antina de Boer, Femke van der Velde, Lisa Brouwer, Dafne Piersma, Floor Rodijk, Renske Lok, Kenney Roodakker and Thom Steenhuis). In addition, the authors would like to thank Dr. Marie-José van Tol and Sonsoles Alonso Martinez, MSc for contributing to the interpretation of the results.
The study was funded by a donation of Mr Hazewinkel to the Research School of Behavioural and Cognitive Neurosciences and Prof G.J. ter Horst. Mr Hazewinkel had no role in study design, data collection and analysis, decision to publish, or preparation of the manuscript.
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Title: using large language models to assist video content analysis: an exploratory study of short videos on depression.
Abstract: Despite the growing interest in leveraging Large Language Models (LLMs) for content analysis, current studies have primarily focused on text-based content. In the present work, we explored the potential of LLMs in assisting video content analysis by conducting a case study that followed a new workflow of LLM-assisted multimodal content analysis. The workflow encompasses codebook design, prompt engineering, LLM processing, and human evaluation. We strategically crafted annotation prompts to get LLM Annotations in structured form and explanation prompts to generate LLM Explanations for a better understanding of LLM reasoning and transparency. To test LLM's video annotation capabilities, we analyzed 203 keyframes extracted from 25 YouTube short videos about depression. We compared the LLM Annotations with those of two human coders and found that LLM has higher accuracy in object and activity Annotations than emotion and genre Annotations. Moreover, we identified the potential and limitations of LLM's capabilities in annotating videos. Based on the findings, we explore opportunities and challenges for future research and improvements to the workflow. We also discuss ethical concerns surrounding future studies based on LLM-assisted video analysis.
Comments: | 6 pages, 2 figures, under review in CSCW 24 |
Subjects: | Human-Computer Interaction (cs.HC); Artificial Intelligence (cs.AI); Computers and Society (cs.CY) |
Cite as: | [cs.HC] |
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