Results are therefore inconsistent with claims in the literature that rats are altruistically motivated to share food with other rats, even when food is abundant

Failure to Find Altruistic Food Sharing in Rats. Haoran Wan, Cyrus Kirkman, Greg Jensen and Timothy D. Hackenberg. Front. Psychol., June 22 2021. https://doi.org/10.3389/fpsyg.2021.696025

Abstract: Prior research has found that one rat will release a second rat from a restraint in the presence of food, thereby allowing that second rat access to food. Such behavior, clearly beneficial to the second rat and costly to the first, has been interpreted as altruistic. Because clear demonstrations of altruism in rats are rare, such findings deserve a careful look. The present study aimed to replicate this finding, but with more systematic methods to examine whether, and under what conditions, a rat might share food with its cagemate partner. Rats were given repeated choices between high-valued food (sucrose pellets) and 30-s social access to a familiar rat, with the (a) food size (number of food pellets per response), and (b) food motivation (extra-session access to food) varied across conditions. Rats responded consistently for both food and social interaction, but at different levels and with different sensitivity to the food-access manipulations. Food production and consumption was high when food motivation was also high (food restriction) but substantially lower when food motivation was low (unlimited food access). Social release occurred at moderate levels, unaffected by the food-based manipulations. When food was abundant and food motivation low, the rats chose food and social options about equally often, but sharing (food left unconsumed prior to social release) occurred at low levels across sessions and conditions. Even under conditions of low food motivation, sharing occurred on only 1% of the sharing opportunities. The results are therefore inconsistent with claims in the literature that rats are altruistically motivated to share food with other rats.

Discussion

The present experiment was designed to replicate and extend some key conditions described by Ben-Ami Bartal et al. (2011), in which rats chose between social release and food. The present research focused on two main findings from that study and their related conclusions: (1) rats chose food and social release with similar latencies, and therefore, food and social release are equally valued; and (2) rats willingly share food with their social partner, even if it comes at a cost to the individual. Taken together, these findings provide key support for the authors' claims of altruistic food sharing. Because occurrences of such unreciprocated food sharing are rare in the published literature (Clutton-Brock, 2009; Taborsky et al., 2016), they warrant further scrutiny.

With respect to the first claim of equal reward value of social release and food, we found that relative value of food and social release varied systematically across conditions. More specifically, when food motivation was low (i.e., the focal rat had unrestricted homecage access to chow in their home cage) and food quantity was high (4–5 pellets per trial), food and social release were chosen about equally often (Conditions 4, 6, and 7), consistent with the (Ben-Ami Bartal et al., 2011) findings. When food motivation was high (restricted access to food outside the session), however, rats clearly preferred food over social release (Conditions 1–3). This finding is consistent with the Hiura et al. (2018) findings, showing strong and reliable preference for food over social release when food is restricted outside the session (see also Blystad et al., 2019). Taken as a whole, the presents results show that relative preference between social and food is not invariant, but rather, is subject to reward and motivational variables (food quantity and overall food access). The relative value of social release and food are always subject to these (and other) variables, and it would therefore be premature to draw broad conclusions about their relative value from sampling only a limited range of conditions. In any case, a motivational view of social and food rewards helps explain discrepant findings from prior research.

The changes in preference across manipulation of food quantity in the first three conditions were driven mainly by changes in the number of food choices per session. This is partly due to economic factors (i.e., decreasing unit price of food) and partly due to satiation. Given the low price (1 response) and the dozens of choice opportunities each session, rats produced and consumed large numbers of sucrose pellets each session when chow in their home cage was restricted (37–284 pellets, mean = 131 across rats). By contrast, when home cage chow was unlimited and food motivation was low, subjects consumed substantially fewer pellets (16–107 pellets, mean = 66 across rats). And when coupled with unlimited food access outside the session in Condition 4, the procedures combined to produce conditions of low food need. Indeed, our rats had such an abundance of food, there was often food left at the end of the food collection periods of Conditions 5–7 (up to 26% of all pellets in Condition 5), even if there was no restrained rat with which to share them. That rats did not consume rewards as highly valued as sucrose pellets suggests a high degree of satiation.

Despite such low levels of food need, there was very little evidence of food sharing – the second and more controversial claim set forth by Ben-Ami Bartal et al. (2011). Behavior that met our operational definition of sharing (i.e., producing food and then releasing the rat while food remained available) was infrequent across all conditions in the experiment, with zero shared pellets being the most common outcome across sessions and the mean being about 1 pellet per session. It did not matter whether food access outside the session was restricted (Conditions 1–3) or not (Conditions 4–7); nor did it matter how many pellets were produced per response (Condition 1–3): rats rarely shared with the other rat any of the abundant supply of food pellets they produced each session. Even in the final two conditions, with procedures that most closely matched the original study (i.e., symmetrically arranged social and food locations, 5 sucrose pellets, and unrestricted access to food and social contact outside the session), sharing was seldom observed (see also Supplementary Video 1). Thus, on the whole, we found no evidence to support the 2011 claim by Ben-Ami Bartal et al. that a rat willingly shares food with another rat.

There is no simple way to reconcile the food sharing reported by Ben-Ami Bartal et al. (2011) with the near complete absence of sharing in the present study. Low levels of food sharing cannot be explained in terms of reduced opportunities for sharing, as the number of social releases (hence, sharing opportunities) remained fairly constant across conditions for individual rats (see Figures 3, 6). This was accomplished by providing repeated exposure to a consistent duration of social contact (30 s) across the experiment. With long sessions and repeated trials, rats had ample opportunities to share the food they had produced; they simply did not do so. The discrepant results also cannot be explained in terms of differing definitions of sharing between experiments. Ben-Ami Bartal et al. (2011) used a less stringent indirect measure of sharing (difference between food consumed with and without a rat available to release) than our behavioral definition of sharing (produce food, then social release with food remaining). This alone cannot be responsible for the different results, however, for even if we adopt the less stringent criterion, our rats showed no differences in food consumption with or without a rat available to release (Figure 7). This is important, as evidence of sharing-related costs are crucial to an altruistic food sharing explanation. Thus, by neither definition did our rats engage in sharing.

We recognize that the present study relies on a small sample size of three rats. Even so, the evidence against food sharing is strong. Across all of the conditions in which sharing was possible, our rats earned an average of 2,171 rewards each (1,662 to 2,772 across rats) of which they shared an average of 47 (0 to 85, across rats), or 1% of the total rewards earned. Because each earned reward provided a sharing opportunity, our rats had vastly greater food sharing opportunities than rats in the Ben-Ami Bartal et al. (2011) experiment. Precise estimates of food sharing opportunities in that experiment are difficult, both because opportunity per reward cannot be derived from the data presented in the paper (% trials with sharing), and because it took the rats several sessions to learn to open the door for either option (before which rewards were not actually available to share). Nonetheless, the theoretical maximum would be 60 food sharing opportunities (five rewards per trial for 12 trials) per rat, roughly 1% of the number food-sharing opportunities in the present study. In addition to vast opportunities for food sharing, the present procedures produced consistent patterns of preferences across animals and over consecutive sessions. Thus, while the small number of rats in the present study limits our ability to generalize to the population of all rats, we have considerable confidence in the results with these particular rats: all were strongly disinclined to share food with their partners across all conditions and thousands of sharing opportunities. Perhaps only some rats engage in altruistic food sharing, differing from their non-sharing conspecifics for some reasons yet to be discovered, and that our sample happened to include only selfish rats who happen to be selfish in very similar ways. This seems unlikely, but it will nevertheless be important to replicate with larger samples of rats in future research.

Another difference between the studies is the food itself. Ben-Ami Bartal and colleagues used a single presentation of 5 chocolate chips, which amounts to approximately 12 calories of food, contained in about 1.62 g. By comparison, each of our sucrose pellets constitutes approximately 0.17 calories, each with a mass of 0.045 g. When subjects had unlimited home cage access to chow, they therefore tended to consume about 11.2 calories of food. Furthermore, rats in Condition 5 (with no opportunity for social access) left about 6 pellets (worth about 1 calorie) behind, despite having no external motivation to do so. This points to subjects with free access to chow leaving high-quality food unconsumed due to satiation, usually doing so shy of 12 calories. If rats with low food motivation are inclined to leave food unconsumed relatively frequently in the absence of conspecifics, it is difficult to argue that losing such food due to sharing can be understood as a “cost.” Ben-Ami Bartal and colleagues give no rationale for their choice of 5 chocolate chips, but based on the patterns of non-social food intake observed in the present study, it seems likely that, had they used 3 chocolate chips, that would have observed almost no sharing, whereas if they had used 7 chocolate chips, they would have observed relatively frequent sharing.

There are other differences between the procedures, and the only way to know for certain which factors are responsible for the discrepant results would be to begin with a direct replication, an exact reproduction of the original procedures, and thereafter change one variable at a time. We chose instead to conduct a systematic replication (Sidman, 1960), in which some, but not all, of the original procedures are reproduced. Systematic replications are useful in assessing the generality of a finding, and this fit with our broader objectives of providing a more thorough characterization of preference and sharing. We sought not only to replicate but to extend, to assess the generality of the findings by exploring behavior across a range of conditions, including but not limited to, those of the original study. In particular, the lack of adequate control conditions leaves the original study open to multiple interpretations. Sampling independent variables under varying conditions puts replication efforts into a broader context, changing the focus from binary questions with yes-no answers (e.g., Do rats value social release over food? Do rats share food with another rat?) toward conditional questions (e.g., Under what conditions is social release favored over food, and vice versa? Under what conditions does sharing occur?). Viewed in this way, Ben-Ami Bartal and collaborators are not so much incorrect as they are interpreting incomplete evidence; their results are part of more general relationships between preference and sharing and the variables of which they are a function.

Exploring such functional relationships across a parametric range can also shed light on theoretical disputes. For example, when examined at only a single point on a function, social release can be interpreted either in terms of social reward (response-contingent access to social interaction) or in terms of empathy (acting out of concern for the other rat): both accounts make the same prediction that door opening will occur. The accounts begin to differ, however, as behavior is examined while other experimental parameters change. For example, in procedures similar to those used here, Vanderhooft et al. (2019) first trained social release in rats, then systematically increased the price of social release (number of responses to produce it) across sessions, generating demand functions. Overall, the functions (27 in all) were well-described by the Hursh and Silberberg (2008) essential value model, a model that has proven useful in quantifying the value of numerous other rewards, including food, water, and drugs (Hursh and Roma, 2016). In other words, rates of social release behavior were predictable, with a high degree of quantitative precision, on the basis of these social reward functions. It is less clear, however, what, if anything, an empathy account would have to say about these data: it makes no obvious predictions about how empathy is affected by price – or other variables known to affect reward value (e.g., magnitude, delay, or probability), about which social reward makes clear and testable predictions. And if predictions could be derived from an empathy account (e.g., by assuming that empathy mirrors social reward functions), they would be indistinguishable from the more parsimonious social reward account, and would therefore add little to the explanation. This is not to deny the importance of empathy as a topic worthy of scientific study; it is, rather, to demand more stringent tests of it, especially in domains in which simpler explanations already exist.

Learning coherence is likely to emerge in individuals and triads, but not in dyads; this coherence in turn leads to higher performance

Harada T (2021) Three heads are better than two: Comparing learning properties and performances across individuals, dyads, and triads through a computational approach. PLoS ONE 16(6): e0252122. https://doi.org/10.1371/journal.pone.0252122

Abstract: Although it is considered that two heads are better than one, related studies argued that groups rarely outperform their best members. This study examined not only whether two heads are better than one but also whether three heads are better than two or one in the context of two-armed bandit problems where learning plays an instrumental role in achieving high performance. This research revealed that a U-shaped correlation exists between performance and group size. The performance was highest for either individuals or triads, but the lowest for dyads. Moreover, this study estimated learning properties and determined that high inverse temperature (exploitation) accounted for high performance. In particular, it was shown that group effects regarding the inverse temperatures in dyads did not generate higher values to surpass the averages of their two group members. In contrast, triads gave rise to higher values of the inverse temperatures than their averages of their individual group members. These results were consistent with our proposed hypothesis that learning coherence is likely to emerge in individuals and triads, but not in dyads, which in turn leads to higher performance. This hypothesis is based on the classical argument by Simmel stating that while dyads are likely to involve more emotion and generate greater variability, triads are the smallest structure which tends to constrain emotions, reduce individuality, and generate behavioral convergences or uniformity because of the ‘‘two against one” social pressures. As a result, three heads or one head were better than two in our study.

Discussion

One of the interesting findings in our study was that a relationship between performance and group size was validated to be U-shaped. As the regression analysis revealed, the causes for this performance difference could be attributed to higher values of the inverse temperatures β in both models. In dyads, group effects regarding the inverse temperatures in both models did not generate higher values to surpass their averages, which might lead to lower performance. In contrast, triads gave rise to higher values of the inverse temperatures than their averages of group members. These differences are responsible for the U-shaped relationship in performance. Although the model selection tests did not differentiate between the simple and asymmetric Q learning models, both shared the same results that the inverse temperature β accounted for higher performance. Thus, our results are robust to model specifications.

At individual levels, participants were more likely to perform the two-armed bandit game in an exploratory manner because their inverse temperatures were relatively lower to dyads and triads. The emphasis on exploration at individual levels indicate that rationality in terms of exploitation in the framework of the underlying learning model increased as more group members were added to the group decision-making processes. To achieve agreement in groups, logical reasoning and persuasion based on rational calculation would be required instead of exploration. Yet, in dyads, this increase in exploitation was not sufficient to make it significantly different from individuals. Indeed, group effects could not generate higher values of β than its averages. It could be inferred that dyads encountered learning incoherence, leading to smaller group effects regarding the inverse temperature.

According to Simmel [59], in dyads, social interaction is more personal, involving more affect or emotion, and generates greater variability. The negative aspect of social interaction seemed to appear in dyads in our experiments. On the other hand, Simmel [59] argued that triads are the smallest structure that tends to constrain emotions, reduce individuality, and generate behavioral convergences or uniformity because of the ‘‘two against one” social pressures. These forces form the basis for uniformity, emergent norms, and cohesion [60]. Consequently, while dyads failed to improve the inverse temperature beyond its average as a result of affective or emotional influences, the smallest social structure, in the form of a triad, improved efficiency due to social pressures and more exploitation. This is also consistent with the theoretical hypothesis in S1 Appendix where dyads are likely to adopt more randomized learning strategies, whereas individuals and triads adopt coherent learning strategies. Although individuals might use more exploratory behaviors, exploration itself is one of the coherent learning strategies. Hence, our empirical results support our hypothesis that learning incoherence takes place in dyads but not in triads.

Notably, the positivity biases were confirmed for individuals and triads, but no such learning biases existed for dyads. As related studies indicated [50–55], learning biases are more likely in such leaerning situations. This result further evidences learning coherence in individuals and triads and learning incoherence in dyads.

Apart from this main result, the fact that group parameters achieved higher values than its means of individual members in most of the learning parameters deserves some attention in its own right. Not only triads, but also dyads, had these positive effects. Future studies should explore these group effects in more detail.

However, our findings are subject to several limitations. First, the results critically depend on the tasks that the groups perform and the learning situations where the TAB games are played. Different game settings could lead to different results. Second, learning properties could change over time through learning, therefore, their reliability might be subject to some limitations. Performance probably changed as participants undertook more TAB games, because of the stochastic nature of the rewards. However, it could be conjectured that its learning strategy tends to be relatively stable because participants could not fully detect the stochastic environments (i.e., which options are more likely to generate higher rewards), as the probability of obtaining higher gains was changed twice during the 100 trials. Hence, it seems that participants were less likely to change their learning strategies even when they undertook the TAB several times. This justifies the use of learning properties in this study. Nevertheless, the reliability of learning properties should be tested in a future study.

Third, although this study used a relatively large sample, different results could be found in different samples, in particular, in different cultural contexts. For example, Shen et al. [61] noted that, when examining the effects of risk-taking on convergent thinking, they found that risk-taking was negatively associated with convergent thinking in China, but these correlations were close to zero or negative in the Netherlands. Thus, cultural effects could alter the learning strategies in the TAB, and hence, the effects of group dynamics on group performance.

Despite these limitations, the findings in this study deserve some attention because previous studies did not evaluate and examine the effects of group dynamics in terms of learning properties. Moreover, the results are intuitive and consistent with the simple hypothesis that the U-shaped relationship with respect to performance emerged due to the coherence of learning strategies. Even though these results might not be supported in different experimental settings; our computational approach could still be applied and is expected to generate new results. Thus, the contribution in this study would be more methodological. This study encourages future research that examines the learning mechanism of group dynamics, according to the computational approach suggested in this study.

Does a 7-day restriction on the use of social media improve cognitive functioning and emotional well-being? Results from a randomized controlled trial show no benefits from a severe screen-time reduction

Does a 7-day restriction on the use of social media improve cognitive functioning and emotional well-being? Results from a randomized controlled trial. Marloes M.C . van Wezel, Elger L. Abrahamse, Mariek M. P.  Van den Abeele. Addictive Behaviors Reports, June 15 2021, 100365. https://doi.org/10.1016/j.abrep.2021.100365

Highlights

• We compared a 10% vs. 50% reduction in social media screen time in a RCT.

• The intervention had no effect on multiple indicators of attention and wellbeing.

• Self-control, impulsivity and FoMO did not moderate the relationships.

• Participants reported improved attention, but behavioral attention did not improve.

• Overall, a more severe screen time reduction intervention does not appear more beneficial.

Abstract

Introduction: Screen time apps that allow smartphone users to manage their screen time are assumed to combat negative effects of smartphone use. This study explores whether a social media restriction, implemented via screen time apps, has a positive effect on emotional well-being and sustained attention performance.

Methods: A randomized controlled trial (N= 76) was performed, exploring whether a week-long 50% reduction in time spent on mobile Facebook, Instagram, Snapchat and YouTube is beneficial to attentional performance and well-being as compared to a 10% reduction.

Results: Unexpectedly, several participants in the control group pro-actively reduced their screen time significantly beyond the intended 10%, dismantling our intended screen time manipulation. Hence, we analyzed both the effect of the original manipulation (i.e. treatment-as-intended), and the effect of participants’ relative reduction in screen time irrespective of their condition (i.e. treatment-as-is). Neither analyses revealed an effect on the outcome measures. We also found no support for a moderating role of self-control, impulsivity or Fear of Missing Out. Interestingly, across all participants behavioral performance on sustained attention tasks remained stable over time, while perceived attentional performance improved. Participants also self-reported a decrease in negative emotions, but no increase in positive emotions.

Conclusion: We discuss the implications of our findings in light of recent debates about the impact of screen time and formulate suggestions for future research based on important limitations of the current study, revolving among others around appropriate control groups as well as the combined use of both subjective and objective (i.e., behavioral) measures.

Keywords: screen timescreen time interventionsustained attentioncognitive performanceemotional well-beingself-report bias

4. Discussion

In the past decade, we have witnessed an increase in studies focusing on the complex associations between the use of the smartphone and its (mobile) social media apps on the one hand, and attentional functioning (Rosen et al., 2013, Judd, 2014, Kushlev et al., 2016, Ward et al., 2017, Wei et al., 2012, Fitz et al., 2019, Marty-Dugas et al., 2018) as well as emotional well-being (Twenge and Campbell, 2019, Twenge et al., 2018, Twenge and Campbell, 2018, Escobar-Viera et al., 2018, Brailovskaia et al., 2020, Tromholt, 2016, Stieger and Lewetz, 2018, Aalbers et al., 2019, Frison and Eggermont, 2017) on the other hand. While research in this field is not without criticism, among others for its over-reliance on self-report data and cross-sectional survey methodologies, the concerns over the potential harm of mobile social media use have nonetheless given impetus to the development of screen time apps that can help people to protect themselves from harm by restricting their social media use. The current study explored the effects of such a social media screen time restriction on sustained attention and emotional well-being.

The findings show that, first of all, the intervention did not have the intended effect. Specifically, we implemented a 50% restriction in social media screen time for an experimental group, and compared this to a control group with a 10% restriction. Yet, this screen time manipulation failed mostly because participants in the control group reduced their social media app use on average with 38%, which was much more than the intended 10%. We deliberately opted to not include a 0% reduction control group in our design, in order to avoid Hawthorne(-like) effects (cf. Taylor, 2004, McCambridge et al., 2014) – hence, in order to provide also the control group participants with a full-blown sense of being involved in an experiment. The current finding that a non-zero percent reduction for a control group may trigger additional – and more problematic – side effects than the Hawthorne(-like) effects that we aimed to prevent with it, is an interesting finding in itself. It provides clear suggestions for optimal implementation of control groups in intervention studies of the current type, and deserves to be followed up as a target of investigation in itself. Indeed, some participants indicated that they felt uncomfortable when encountering a time limit. It is imaginable that participants reduced their screen time more than they needed to in order to avoid that situation. Alternatively, the failed manipulation may be due to a placebo effect (cf. Stewart-Williams & Podd, 2004). In this case, the mere expectation of receiving a social media reduction may have sufficed in promoting behavior change in the form of reduced social media use. Similar placebo effects were found in marketing research (Irmak, Block, & Fitzsimons, 2005).

To deal with the failed screen time manipulation, we provided analyses both for treatment-as-intended and treatment-as-is, with the latter set of analyses disregarding the intervention conditions but rather exploring linear associations between the degree of relative screen time reduction based on the data we obtained. Interestingly, neither analyses revealed a noticeable effect on the outcome measures. This finding suggests an alternative explanation for the lack of findings, namely that there may not be any negative association between social media screen time and the outcome measures to begin with. Indeed, the pre-test data – which are unaffected by the failed screen time manipulation – did not show any of the hypothesized correlations between social media screen time, emotional well-being and attentional performance. On the contrary, the only relationships found between social media screen time and the outcome measures ran counter to what one might expect: Heavier social media users reported experiencing less attentional lapses and negative emotions. The lack of any negative association between social media screen time and the outcome measures may explain why reducing this screen time has no causal impact: If social media screen time does not affect these outcomes much, altering it will unlikely cause much change in them.

This finding is interesting in light of recent debates in the field over the validity of screen time studies. A recurring concern voiced in these debates is that self-report measures of screen time are flawed to such an extent that their use can lead to biased interpretations (Kaye et al., 2020, Sewall et al., 2020). A key strength of the current study is that we used a behavioral measure of screen time. The fact that this measure shows no relationship to cognitive performance nor emotional well-being, calls into question the ‘moral panic’ over social media screen time (Orben, 2020).

An alternative explanation that should be mentioned here, is that despite the randomization of participants, the control and experimental group were not fully equivalent in terms of their smartphone behavior in the week prior to the experiment. The control group appeared to consist of heavier Instagram users whereas the experimental group consisted of heavier WhatsApp users. It is thinkable that this non-equivalence has had some influence on our findings. After all, for the light Instagram users in the experimental group, a 50% reduction in Instagram use may not have been very impactful, whereas for the heavy Instagram users in the control group, the actually enforced relative reduction of 35% may have had a more profound impact, thus leveling out any difference between the two groups. Future researchers thus need to carefully consider their experimental procedures to maximize the chances of equivalence between conditions.

While we believe that a strength of our current study is the use of actual smartphone data and performance based measures of attention, the paucity of the use of such measures in previous work prevented us from conducting an appropriate a priori power analysis, resulting in a sample size that may have been too small – as indeed indicated by for example the accidental but significant differences between conditions in terms of their baseline app use (see above). We hope that our study can serve to that purpose in the future.

While the manipulation did not resort an effect, the findings of our study did show that – disregarding of the condition they were in – people reported experiencing less cognitive errors and attentional lapses at the post-test. This is interesting, given that their actual attentional performances did not improve. Again, these findings are interesting in light over the recent debates over the use of self-report measures in research on the associations between screen time and psychological functioning. Recent studies show that the use of self-report measures leads to an artificial inflation of effect sizes of these associations (Sewall et al., 2020, Shaw et al., 2020), that self-reports of especially smartphone use are inaccurate (Boase and Ling, 2013, Ellis et al., 2019, Vanden Abeele et al., 2013), and that the discrepancies between self-reported and behavioral measures of smartphone use are themselves correlated with psychosocial functioning (Sewall et al., 2020). The mixed findings in research on the effects of screen time have led to a call for greater conceptual and methodological thoroughness (e.g., Whitlock and Masur, 2019, Kaye et al., 2020, Sewall et al., 2020, Shaw et al., 2020), with a specific call to prioritize behavioral measures over self-report measures. The discrepancy between the behavioral and self-report attention measures may be an artifact of this shortcoming of self-report methodology.

The null-results of FoMO, self-control and impulsivity as influential moderators should be elaborated on here. It was expected that a screen time intervention would negatively impact the emotional well-being of individuals, especially those high on FoMO, since reduced social media screen time also reduces the possibility to stay up-to-date. However, our results could not corroborate this notion. Several authors have suggested that rather than being a predictor of social media use, FoMO may be a consequence of such online behavior (e.g., Alutaybi, Al-thani, McAlaney & Ali, 2020; Buglass, Binder, Bets, & Underwood, 2017; Hunt et al., 2018). In the three-week intervention study of Hunt et al. (2018) for example, reduced social media use actually reduced feelings of FoMO. With our data, we could test this possibility. Hence, we executed a repeated measures ANOVA with FoMO as within-subjects factor and condition as between-subjects factor. This analysis revealed that the intervention had no significant effect on experienced FoMO (i.e., the experimental group did not experience larger changes in FoMO than the control group: F(1,74)= 0.09, p=.762). However, there was an effect of time on FoMO: at the post-test, FoMO was significantly lower than at the pre-test (Mdif = 0.18, F(1,74)= 6.65, p= .012). Perhaps this is indicative of an “intervention effect”, since our manipulation had failed and all participant significantly reduced their social media use during the intervention week.

Also, an overall finding of this study, which aligns with what prior research has found, was that participants were not able to estimate their screen time accurately: While participants’ actual screen time decreased during the intervention week, their self-reported screen time did not differ over time. Interestingly, participants did report a decrease in habitual use and problematic use. This may suggest that people may have a vague sense of their behavior (“I reduced my smartphone use”), but are unable to convert this adequately into numbers such as screen time in minutes. Alternatively, participants may have provided a socially desirable answer. Either case, our findings aligned with both recent and older studies showing that subjective screen time measures deviate from objective measures (e.g., Andrews et al., 2015, Boase and Ling, 2013, Vanden Abeele et al., 2013, Verbeij et al., 2021).

4.1. Limitations and Future Directions

This study is among the first to examine the effectiveness of a social media screen time reduction on sustained attention and emotional well-being. One of its strengths is the inclusion of behavioral measures, both for screen time and for sustained attention. The study is not without limitations, however. A number of methodological choices were made that significantly limit comparability with other findings in the field. The lack of a true control group (in which no intervention was implemented) and the limited sample size are major limitations to the current study. Future research should include more participants and should consider the use of a true control group, in which no intervention is implemented. Moreover, future research might look at different degrees of screen time reductions, ranging from no reduction to complete abstinence, to better address to what extent the magnitude of the restriction matters. To add, future work ought to consider how to account for individuals’ unique smartphone app repertoires. For instance, some individuals in our study were super users of mobile games rather than of social media. While this may lower generalizability, researchers might account for unique app repertoires by setting time restrictions on an individual’s top 5 apps, or on screen time in-total. Also, a one-week intervention is short. It is likely that a longer intervention is needed to produce an effect on the outcomes examined. Overall, a general observation that we make is that future research on screen time interventions needs to carefully question and compare (1) which types of interventions affect (2) which outcomes, (3) for whom and (4) under which conditions, and (5) because of which theoretical mechanisms.

An additional limitation is that, although they were kept blind about which condition they were in, participants were informed about what the experiment was about because willingness to set a restriction to one’s screen time was an important eligibility criterion; installing such a timer without the participants’ informed consent was deemed unethical. Given that the timers were installed on participants’ personal phones, it was easy for participants to look up what restriction was enforced on them. Future research might explore if participants can be kept in the blind. Perhaps this can be attained via the development of a screen time app tailored to this purpose. Notably, even though we found no increase in the use of social media on alternative devices, it should be acknowledged that social media can be accessed from other devices than smartphones alone, something that could be accounted for in future work. In this context, it is relevant to mention Meier and Reinecke’s (2020) taxonomy of computer-mediated communication. Meier and Reinecke advice researchers to carefully consider which level of analysis they are focusing on, most notably that of the device (i.e., a ‘channel-based’ approach) versus that of the functionality or interaction one has through the device. Decisions regarding the level of analysis are typically grounded in theoretical assumptions about the mechanisms explaining effects. We consider this observation relevant to researchers studying ‘digital detoxes’ or screen time interventions, as they similarly have to consider what it is exactly that they want participants to ‘detox’ from, the device, a particular app or functionality, or a type of interaction. Careful consideration of this issue is important, as it may be key to understanding why the extant research shows mixed evidence. In the current study we attempted to address the type of interaction people have with social media, targeting especially ‘passive social media use’ by enforcing only a partial restriction, but we only focused on mobile social media. Future researchers may wish consider more explicitly their level of analysis and how to operationalize it in an intervention.

Finally, as other research also shows (e.g., Ohme, Araujo, de Vreese, & Piotrowski, 2020), research designs that include behavioral measures of smartphone use are both ethically and methodologically challenging. In the current study, we only invited participants to the lab with smartphones running on recent versions of IoS or Android. However, some participants showed up unaware of the operating system of their phone. Others used older versions, on which the screen time monitoring features did not function, or had forgotten to activate the screen time monitoring feature prior to the baseline measurement (which we had also specified as an eligibility criterion). This led to exclusion of several participants. Additionally, in a pilot study of the experiment, we noticed that different phone brands and types use different interfaces to display screen time information. This led to confusion, for instance, over whether the displayed numbers were weekly or daily totals. Hence, to avoid errors, we chose not to let participants record their own screen time but rather explicitly asked participants to hand over their phone to a trained researcher who copied the information into a spreadsheet and installed the timers. Participants who felt uncomfortable with this procedure were invited to closely monitor the researcher, or – if desired – to navigate the interface themselves. Although only a handful of students chose this option, this shows that there are ethical implications to using data donation procedures that researchers have to consider.

To circumvent these issues in future studies, participants could be instructed to install the same app. However, this will increase the demands placed on participants. Participation in studies of this nature are already highly demanding and intensive, since participants have to undergo a multi-day intervention on behavior that is intrinsic to their daily lives, and with sharing of personal information. Additionally, asking participants to install a specific app that potentially remotely monitors their phone use can raise ethical concerns, especially when using a commercial app that makes profit of monitoring (and selling) user data.

Overall, it became clear that it is difficult to achieve the required sample size to investigate complex designs of this nature. Nonetheless, the contrasting findings in extant research call for more research on causal relations between social media use on the one hand, and emotional well-being and cognitive functioning on the other hand. This can only be achieved by the use of slow science and large resources.

Check also Reasons for Facebook Usage: Data From 46 Countries. Marta Kowal et al. Front. Psychol., April 30 2020. https://doi.org/10.3389/fpsyg.2020.00711

Sex Differences

Are there sex differences in Facebook usage? According to Clement (2019), 54% of Facebook users declare to be a woman. Research conducted by Lin and Lu (2011; Taiwan) showed that the key factors for men's Facebook usage are “usefulness” and “enjoyment.” Women, on the other hand, appear more susceptible to peer influence. This is concurrent with the findings of Muise et al. (2009; Canada), in which longer times spent on Facebook correlated with more frequent episodes of jealousy-related behaviors and feelings of envy among women, but not men. Similarly, in Denti et al. (2012), Swedish women who spent more time on Facebook reported feeling less happy and less content with their life; this relationship was not observed among men.

In general, women tend to have larger Facebook networks (Stefanone et al., 2010; USA), and engage in more Facebook activities than men do (McAndrew and Jeong, 2012; USA; but see Smock et al., 2011; USA, who reported that women use Facebook chat less frequently than men). Another study (Makashvili et al., 2013; Georgia) provided evidence that women exceed men in Facebook usage due to their stronger desire to maintain contact with friends and share photographs, while men more frequently use Facebook to pass time and build new relationships.

Effects of Evolution, Ecology, and Economy on Human Diet: Insights from Hunter-Gatherers and Other Small-Scale Societies

Effects of Evolution, Ecology, and Economy on Human Diet: Insights from Hunter-Gatherers and Other Small-Scale Societies. Herman Pontzer and Brian M. Wood. Annual Review of Nutrition  Volume 41, on-line June 17, 2021. https://doi.org/10.1146/annurev-nutr-111120-105520

Abstract: We review the evolutionary origins of the human diet and the effects of ecology economy on the dietary proportion of plants and animals. Humans eat more meat than other apes, a consequence of hunting and gathering, which arose ∼2.5 Mya with the genus Homo. Paleolithic diets likely included a balance of plant and animal foods and would have been remarkably variable across time and space. A plant/animal food balance of 40–60% prevails among contemporary warm-climate hunter-gatherers, but these proportions vary widely. Societies in cold climates, and those that depend more on fishing or pastoralism, tend to eat more meat. Warm-climate foragers, and groups that engage in some farming, tend to eat more plants. We present a case study of the wild food diet of the Hadza, a community of hunter-gatherers in northern Tanzania, whose diet is high in fiber, adequate in protein, and remarkably variable over monthly timescales.

Check also Although we are undoubtedly omnivores, we evolved quite early to become highly carnivorous and we continue to retain a biologic adaptation to carnivory:

Ben-Dor, Miki (2019) "How carnivorous are we? The implication for protein consumption," Journal of Evolution and Health: Vol. 3: Iss. 1, Article 10. https://www.bipartisanalliance.com/2019/03/although-we-are-undoubtedly-omnivores.html

Do Local Sex Ratios Approximate Subjective Partner Markets? There is a need for more fine-grained, age-specific sex ratios

Do Local Sex Ratios Approximate Subjective Partner Markets? Evidence from the German Family Panel. Andreas Filser & Richard Preetz. Human Nature, Jun 19 2021. https://link.springer.com/article/10.1007/s12110-021-09397-6

Abstract: Sex ratios have widely been recognized as an important link between demographic contexts and behavior because changes in the ratio shift sex-specific bargaining power in the partner market. Implicitly, the literature considers individual partner market experiences to be a function of local sex ratios. However, empirical evidence on the correspondence between subjective partner availability and local sex ratios is lacking so far. In this paper, we analyzed how closely a set of different local sex ratio measures correlates with subjective partner market experiences. Linking a longitudinal German survey to population data for different entities (states, counties, municipalities), we used multilevel logistic regression models to explore associations between singles’ subjective partner market experiences and various operationalizations of local sex ratios. Results suggest that local sex ratios correlated only weakly with subjective partner market experiences. Adult sex ratios based on broad age brackets, including those for lower-level entities, did not significantly predict whether individuals predominantly met individuals of their own sex. More fine-grained, age-specific sex ratios prove to be better predictors of subjective partner market experiences, in particular when age hypergamy patterns were incorporated. Nevertheless, the respective associations were only significant for selected measures. In a complementary analysis, we illustrate the validity of the subjective indicator as a predictor of relationship formation. In sum, our results suggest that subjective partner availability is not adequately represented by the broad adult sex ratio measures that are frequently used in the literature. Future research should be careful not to equate local sex ratios and conscious partner market experiences.

Discussion

Imbalanced sex ratios have been linked to a wide range of social consequences, including family formation, economic decision-making, gender roles, partnership formation, fertility, personality, and sexuality (Bauer & Kneip, 2013; Feingold, 2011; Griskevicius et al., 2012; Harknett, 2008; Merli & Hertog, 2010; Pollet & Nettle, 2008; Schacht & Smith, 2017; Trent & South, 2012; Uggla & Mace, 2017). Sociodemographic and evolutionary mating market approaches have explained these findings by shifts in bargaining power based on differential mating opportunities for men and women in an imbalanced sex ratio environment (Filser & Schnettler, 2019; Guttentag & Secord, 1983; Kokko & Jennions, 2008; Pedersen, 1991; Schacht & Kramer, 2016). Individual partner market experiences might play a crucial role in these behavioral adaptations to local sex ratios given that subjective experiences provide critical guidelines for human behavior (Gilbert et al., 2016; Gintis, 2006; Kroneberg & Kalter, 2012). Yet, empirical evidence has been lacking on how closely individual experiences of partner market opportunities correspond to sex ratios of their local environment. To fill this gap, we analyzed associations between a variety of local sex ratio measures and subjective partner market experiences of female and male singles in a German panel survey.

In sum, the expected association between subjective partner market experiences and local sex ratios only held for selected, age-specific sex ratio measures. In particular, adult sex ratios based on broad age ranges as are commonly used in the literature did not prove to be significant predictors of subjective partner market experiences. This result was consistent across operationalizations of adult sex ratios as the proportion of men in the adult population (PMA) based on different age brackets at the level of states, counties, and municipalities. None of the adult sex ratio variants correlated with either men’s or women’s subjective experiences of surplus encounters with individuals of their own sex in a meaningful way. More granular, age-specific sex ratio measures (ASPM) that include only individuals of adjacent age cohorts were closer approximations of subjective partner market experiences. In particular, age-specific measures that also incorporated age shifts to reflect age hypergamy patterns proved to be better predictors of subjective partner market experiences. Nevertheless, only selected state-level, age-shifted sex ratios correlated with women’s surplus encounters with other women in a statistically significant way. The corresponding county-level age-shifted sex ratios yielded similar, yet smaller coefficients, which have to be interpreted with caution given that they did not reach statistical significance. For men, only county-level, age-shifted sex ratios significantly predicted associations with men’s subjective partner market experiences. Coefficients for state-level age-shifted sex ratios were similar in size but did not reach statistical significance. Overall, some reservations regarding the state-level findings seem warranted because the German states might be too large in geographic terms (with all but four being larger than 15,000 km2) to be considered a single partner market. Lengerer (2001:142) reports that 85% of future partners in Germany live within a 20 km radius of each other. Recent publications suggest that earlier recommendations to rely on smaller entities when operationalizing local partner markets continue to apply in the age of Internet dating (Bruch & Newman, 2019; Fossett & Kiecolt, 1991). Therefore, results for state-level sex ratios should be treated with caution.

In sum, the results of this study suggest that previous findings regarding the social consequences of imbalanced sex ratios are unlikely to be mediated by conscious adaptations to partner scarcities or oversupplies. Adult sex ratios for fixed age brackets, such as the population aged 16–49 or 16–64, constitute the standard operationalization of local sex ratios in the literature (see Schacht et al., 2014; Pollet et al., 2017 for reviews). Our findings suggest that sex ratios for fixed adult age ranges are unlikely to correspond closely to subjective partner market experiences. Previous research has demonstrated that sex ratios correlate only moderately with each other when different age cutoffs are used (see Fossett & Kiecolt, 1991 for a discussion using US census data). Therefore, adult sex ratios are unlikely to be a well-suited summary measure of age-specific sex ratios. This is also supported by our dissimilar results for adult and age-specific sex ratios. In contrast to adult ratios, selected age-specific and age-shifted operationalizations significantly predicted subjective partner market experiences. In particular, the integration of age hypergamy into the sex ratio measures yielded significant results for predicting subjective partner market experiences. Future research should therefore consider focusing on age-specific, age-shifted sex ratio measures. Yet, although age-shifted sex ratios predicted men’s subjective partner market experiences, we only find weak evidence for a similar association for women. This difference between men and women might be due to a smaller sample size of women in our models. A further explanation could be related to sex differences in sexual strategies guiding partner market behavior. In particular, sexual strategies theory suggests that sexual selection favored antagonistic mating competition and preferences for multiple short-term mating in men (Buss, 1999; Schmitt, 2015; Trivers, 1972). This could also entail that men are more aware of marriage squeezes than women are.

A further finding of this paper is that subjective surpluses of same-sex encounters significantly predicted relationship formation. For both sexes, a subjective surplus of encounters with individuals of one’s own sex was significantly associated with a lower probability of entering a relationship. We are aware that survey questions on subjective partner market experiences may represent an excessive demand for respondents. However, the fact that the subjective indicator correlates with this specific partner market outcome supports the idea that the analyzed reports of surplus encounters with same-sex individuals constituted a valid approximation of individual partner market experiences. Concerning the local sex ratio measures, age-specific and age-shifted variants proved to be advantageous over adult sex ratios also when predicting relationship formation. None of the adult sex ratios significantly predicted relationship formation. Moreover, age-specific local sex ratios only yielded significant coefficients when incorporating age shifts. Specifically, relationship formation for women was significantly predicted by state- and county-level age-specific and age-shifted sex ratios. Yet, the probability of men entering a relationship was not predicted by local sex ratios, replicating similar asymmetric findings by Uggla and Mace (2017). With regard to the link to subjective partner market experiences, our findings suggest that subjective partner market experiences and local sex ratios should be considered distinct context variables rather than equivalent indicators. This is even true for detailed measures of local sex ratios. For instance, age-specific county-level sex ratios with a two-year age shift were a significant predictor of women’s relationship formation. Yet, we do not find conclusive evidence that these measures were correlated with women’s subjective partner market experiences. Consequently, these findings suggest that subjective and local sex ratios are not interchangeable operationalizations. Rather, they appear to be two separate dimensions of partner market circumstances. Researchers should be aware of this distinction when offering theoretical interpretations of results based on local sex ratios.

The subjective partner market indicator used in this study is not equivalent to the situational perception of the sex proportions in a group. Instead, it approximated the everyday interactions of individuals and therefore should not be interpreted as indicative of an inability to perceive sex ratios in set groups. Both Alt et al. (2017) and Neuhoff (2017) demonstrated that participants are able to give accurate sex ratio estimations based on short-term exposure to visual and auditory cues. Against the backdrop of these previous studies, one potential explanation for our findings could be that individual partner market experiences are not a direct representation of macro-structural conditions, i.e., local sex ratios (Blau, 1977; Rapp et al., 2015; Schwartz, 1990). Instead, individual partner markets may be structured in different “foci of activity,” such as workplaces, voluntary associations, or hangouts (Feld, 1981; Rapp et al., 2015). With this in mind, studying the consequences of sex ratios in interactive spheres such as workplaces (Åberg, 2009; Barclay, 2013; Svarer, 2007), industries (Uggla & Andersson, 2018), bars (Lycett & Dunbar, 2000), or colleges (Harknett & Cranney, 2017) would have the advantage of assuming that the individuals are actually interacting with one another. This is much more plausible than the same contention would be for local sex ratios. Consequently, individuals’ foci-specific sex ratios might give a more accurate impression of partner supply and demand within the respective foci rather than sex ratios of the local population, even for their specific age cohort.

This paper used a combination of administrative population information and survey data, which is crucial to this analysis. Studies relying on such data face a trade-off between the scope of the data and the ability to link survey data with survey-based partner market measures. The pairfam survey data constitute a unique combination of both ends of this spectrum. However, adult sex ratios in Germany may not have sufficient variation to allow for identifying a clear effect. This is particularly true for adult sex ratios at the state level, which only range between 96 and 108 men per 100 women (see Table 2). Consequently, nonsignificant findings for state-level sex ratios could also be due to the lack of variation at this level of aggregation. Internationally, local adult sex ratios may vary more substantially in selected regions, most notably in the male-skewed populations of China and India (Guilmoto, 2012). However, the county-level variation in adult sex ratios in the analyzed data was consistent with that of recent studies from other Western countries (e.g., Schacht & Kramer, 2016), and the ranges of age-specific sex ratios exceeded the ranges of adult sex ratios in our data.

A further limitation is that the findings are contingent on the validity of the subjective partner market indicator. While our complementary analysis demonstrated the predictive validity of the subjective indicator with respect to relationship formation, limitations persist. The directional verbalization of the indicator question introduced ambiguity, resulting in imprecise measurement of undecided and disagreeing answers. Specifically, respondents who met an equal number of men and women either might have reported disagreeing with the statement of predominantly meeting individuals of their own sex or might have given an undecided answer to express their experience of a balanced sex ratio. We explored this issue via fitting linear and multinomial models for different variants of the original indicator scale. These auxiliary results confirmed that the difference in probabilities for undecided and disagreeing answers was not significantly correlated to local sex ratios. However, agreement with the surplus same-sex contacts scale was related to selected local sex ratio measures (Fig. S6-S8, in the ESM). We therefore focused on the dichotomized indicator that summarized disagreeing and undecided responses. Nevertheless, our logistic regression results do not persist when taking a linear modeling approach, most likely because of measurement noise in disagreeing and undecided responses. Furthermore, the current analysis was limited to one global subjective indicator of opposite-sex encounters. A detailed survey of foci-specific sex ratios might give a closer approximation of subjective partner market experiences (cf. Rapp et al., 2015). This could reveal whether partner markets in specific foci actually correspond to local sex ratios, whereas partner markets in other foci do not. In particular, detailed information on job location could be of particular relevance, given that 60% of German employees cross municipality borders when commuting (Pütz, 2017). Consequently, adding sex ratios based on the place of work could yield a higher correspondence to subjective partner markets.

In conclusion, the sex ratio literature should be cautious regarding the assumption that individuals are consciously aware of local sex ratio skews. In particular, subjective and conscious partner market experiences do not appear to be a direct function of broad-range adult sex ratios but instead are correlated only with selected, age-specific measures. Researchers should consider this when interpreting findings based on local sex ratios. Although our findings shed some doubt on a direct link between conscious experiences and local sex ratios, this does not necessarily imply that local sex ratios do not capture partner markets. So far, very little is understood about how humans experience, remember, and process contextual sex ratios (Dillon et al., 2017). In particular, the relative importance of immediate interaction partners, local communities, and broader social contexts is yet to be explored (Maner & Ackerman, 2020).

This paper explored the relationship between a general indicator of subjective partner market experiences and local sex ratio measures. In sum, general sex ratio measures that are based on broad age ranges do not seem to capture conscious partner market experiences in a meaningful way. Future research will have to establish the role of unconscious factors, including endocrinal or network effects mediating contextual local sex ratios and adaptations in individual behavior.