Birth in the Time of Corona: Excess Infant Deaths in Nigeria during the COVID-19 Pandemic

Abstract

The COVID-19 pandemic has put severe pressure on health care systems worldwide. While, understandably, attention has been focused on COVID-19 hospitalizations and deaths, some experts have warned about potentially devastating secondary health effects. These effects may be most severe in low and middle-income countries with already weak health systems. This study examines the effect of the COVID-19 pandemic on early infant deaths. There is disagreement about whether, and to what extent, the pandemic has affected infant deaths. Importantly, there is almost no evidence from sub-Saharan Africa, where 2 in every 5 newborn deaths worldwide occur. This study presents new evidence from Nigeria showing that early infant deaths have significantly increased during the pandemic. Using data on the birth outcomes of a large diverse cohort of pregnant women enrolled in a prospective study and a quasi-experimental difference-in-difference design, we find a 1.1 (22% relative increase) and 0.72 percentage-point increase (23% relative increase), respectively, in stillbirths and newborn deaths.

Our findings show that the health effects of the pandemic extend beyond counted Covid-19 deaths. If these findings generalize to other low and middle-income countries, they may indicate that the hard won gains in child survival made over the last two decades are at risk of being reversed amidst the ongoing pandemic. Policies addressing disruptions to health service delivery and providing support to vulnerable groups, and specifically households with pregnant women, will be critical as the pandemic continues.

INTRODUCTION

The challenges of giving birth during the COVID-19 pandemic have received wide coverage in the popular press (1,2). Childbirth is a critical time, with majority of child deaths occurring within a few days of birth (3,4). Leading organizations such as the United Nations International Children’s Emergency Fund (UNICEF) have sounded the alarm about potential adverse impacts of the pandemic (5). Some scholars have issued similar warnings (6,7). However, robust empirical evidence is hard to come by. Notably, there is scant evidence from low and middle-income countries, where nearly all child deaths occur, and where health systems may be least equipped to deal with the fallout of the pandemic (8).

There has been some speculation that the SARS-CoV-2 virus might affect birth outcomes directly, e.g., through maternal infection and vertical transmission, but the available evidence suggests that these direct effects are likely small (9,10). Adverse effects, to the extent that these are present, are more likely going to be a consequence of the indirect effects of the pandemic, e.g., as a result of individual, health system, and policy responses (11). For example, pregnant women might not seek care for fear of becoming infected, government mandated stay-at-home orders might make it more difficult to access care, or pandemic-related disruptions to service delivery might lead to worse care and worse outcomes. There is some disagreement as to whether child outcomes have worsened. Some early research suggested that stillbirths may have increased during the pandemic (12,13), but this finding has been disputed by later work (14,15).

This paper presents new evidence from Nigeria. Nigeria, notably, is a leading contributor to global child deaths, accounting for about 10% and 12%, respectively, of all neonatal deaths and stillbirths (3,16). Like other poorer countries, Nigeria appears to have largely been spared from the direct effects of the SARS-Cov-2 virus—the reasons for this are debated (17). As of January 31, 2021, there were 131,242 total confirmed cases, and 1,586 documented deaths, among a population of more than 200 million (18), though this is almost certainly an undercount (19). Counting only deaths from COVID-19, however, may severely understate the mortality effects of the pandemic. A key question, for poorer countries like Nigeria that may have escaped the direct brunt of the pandemic, is whether there are indirect mortality impacts that are not being measured. This is a particularly important consideration given the weak health systems in these countries. A death due to the COVID-19 pandemic is just as much a death as one from COVID-19. These ‘collateral deaths’, if present, need to be measured and, where appropriate, mitigation strategies devised.

This paper leverages data from a, serendipitously well-timed, prospective study in Nigeria. This study enrolled a large diverse cohort of pregnant women drawn from more than 1,300 communities. Enrollment took place between July 2019 and April 2020, and women gave birth between August 2019 and November 2020. We, thus, observe births before, and after, the start of the pandemic in Nigeria. Additionally, at enrollment, we collected historical birth data from all study participants, which allowed us to further compare changes in outcomes in 2020 to the same changes in previous years for the same participants. This robust quasi-experimental design addresses a number of key potential confounders. A key strength of this study is that we observe outcomes for all births, regardless of where the birth took place. This is noteworthy because, in poorer countries, a large fraction of births occur outside of health facilities; additionally, the pandemic may have led to changes in health care utilization that make it problematic to draw conclusions based on institutional births (20).

We believe that the findings from this study will be informative as policymakers continue to grapple with the effects of the pandemic.

STUDY DATA AND METHODS

Setting

The first cases of COVID-19 in Nigeria were confirmed in March 2020 in Lagos, the commercial center, primarily among recent international travelers (21). In response, international flights were suspended on March 23. By April, there was evidence of community spread with cases confirmed in multiple states, and strict stay-at-home orders were instituted across the country (21). These were lifted in May/June, replaced by much less restrictive night-time curfews. By September/October, life had largely returned to normal, with only a few hundred cases being reported daily (international flights resumed in September). As of the time of writing, however, a second wave appears to have begun in December, 2020. A graphic showing case counts in Nigeria over time is included in the online Appendix (22). This paper focuses on the first wave: our data extend to November 2020.

Study participants

This study uses data from a large prospective study in Nigeria. The study was conducted in 288 Primary Health Service Areas (a Health Service Area consists of communities served by a public primary health center). The 288 Service Areas were drawn from four states (72 Service Areas per state). Two states were selected from the northwest region of Nigeria (Kano and Jigawa), and one each from the northeast and south-south regions (Gombe and Akwa Ibom respectively); the sample is therefore quite diverse. Table A.1 (22) shows selected maternal and child health indicators by region. We also compare sample means to Nigeria averages. As you can see the sample is quite similar (on these characteristics) to Nigeria as a whole (which makes sense given that the sample is drawn from across multiple regions).

The four specific states in these regions were purposively selected based on feasibility of project implementation. The specific Service Areas in each state were selected with the help of government health officials. They are broadly distributed across each state and should be considered representative. The main selection criteria used, in addition to distribution across the state, was that the public health center in the community offered delivery services.

Approximately 120 pregnant women were randomly selected from each Service Area and enrolled in the prospective study. To recruit women in a Service Area, we first randomly selected a community within the Service Area and then conducted a door-to-door census to identify all pregnant women in the community. Pregnancy was the only eligibility criterion. All pregnant women, who gave consent, were enrolled in the study (the refusal rate was < 0.1%). We repeated this process — randomly selecting another community, conducting a census, and enrolling all women — until we reached the desired target number of approximately 120 women. Enrollment took place between July 2019 and April 2020.

Enrolled women received two primary interventions: an information intervention in which participants received information at enrollment about pregnancy risk factors, and another intervention in which participants were offered modest incentive payments conditioned on using prenatal and delivery care. Participants were informed about the incentives at enrollment, with payment made after delivery. These interventions were randomized at the Service Area level, so all women in the same Service Area received the same intervention.

The interventions were cross-cut: study clusters were first assigned with equal probability to the information/no information treatment. Independently, clusters were then randomly assigned to the incentive/ no incentive groups, stratifying by information. The design thus creates four groups: no intervention, risk information, incentives, and risk information + incentives. There are 72 study clusters in each group. This paper is not about the program interventions themselves, but to account for their effects we include a dummy for each group in the statistical model.

Data

All study participants completed an enrollment interview during which we collected demographic information and a full retrospective birth history. For each prior birth we know whether the child was stillborn or liveborn; and for liveborn children who died after birth, we have information about the month and year of death and age at death allowing us to reconstruct mortality history for prior births. During the enrollment interview, we also collected information about household characteristics that are used as control variables.

Study participants completed a follow-up interview approximately four months after delivery. These interviews were conducted in women’s homes. This interview collected information about health care utilization during the current pregnancy and the outcome of the pregnancy. For this child, we observe whether they were alive at follow-up and, if not, when they died. All interviews were conducted by trained data collectors employed by a local university.

Outcomes

The primary outcomes are stillbirths and newborn deaths. A stillbirth is a birth after 24 weeks of gestation where the child showed no signs of life. A newborn death is a death of a liveborn child within the first month of life (to account for women’s tendency to round).

Statistical Analysis

We use a difference-in-difference estimation strategy. We compared mortality for children born during the pandemic to those born in the months before the pandemic (first difference), to the same change in prior years using data from women’s birth histories (second difference). We defined births between April and November 2020 as during the pandemic (the exposed group). Births between December and March constitute the unexposed group. December 2019 to November 2020 makes up one (non-overlapping) year. Births in the five years preceding enrollment are used as a comparator. The comparator period runs from December 2013 to November 2018. Our empirical strategy, therefore, calculates the change in mortality between December-March (unexposed births) and April-November (exposed births) in 2020 and compares this to the change in mortality between December-March and April-November in the five preceding years (2014–2018).

This double-difference strategy is robust to a number of potential confounders. One approach, that has been used in this literature, is to take a difference between exposed and unexposed births in 2020. However, if births between April and November are different than births between December and March, i.e., a seasonal effect, this is confounded with the estimated effect of the pandemic (23). To take out this seasonal effect we, first, calculate the difference between exposed and unexposed births in prior years, and then compare it to the same difference in 2020. This design also controls for temporal trends. An alternative approach that has been used is to compare exposed births in 2020 to births over the same period in prior years, but separating the effects of the pandemic from the effects of naturally occurring trends is difficult. Our empirical strategy also accounts for this as we can separate out the effect of temporal trends using unexposed births in each year.

One can calculate a difference-in-difference by hand from a 2 × 2 table, as we will show, but we will also estimate it using a linear probability regression model, which allows us to account for the study design and to include covariates. The key explanatory variable is the interaction between the exposure and treated/comparator period indicators (EXPOSED x TREATED). We include state fixed effects (24), and a full set of year and calendar month-of-birth dummies that flexibly control for temporal trends and seasonal effects respectively.

Covariate-adjusted models add in individual-level covariates including mother’s age, ethnicity, religion, education, and household wealth quintiles (for details see Appendix) (22). We also control for the child’s sex, which is known to be correlated with mortality (25). Finally, to account for the effect of the study interventions, we include interactions between each intervention group and the treated/comparator period indicators. Later on, we will examine whether the interventions modified the effect of the pandemic. Standard errors are clustered at the level of the Service Area. The Appendix includes sensitivity results where standard errors are clustered at the community level. The results are similar.

Ethical Approval

Ethical approval for the study was given by RAND’s Human Subjects Protection Committee and by the Ethics Committee of Aminu Kano Teaching Hospital, Nigeria.

Limitations

Our results should be interpreted in light of the study’s limitations. First, our retrospective data is based on recall, which may lead to some reporting error. Second, the difference-in-difference estimator relies on what is known as the parallel trends assumption which, ultimately, is untestable; but we will present visual evidence suggesting that it plausibly holds in this setting. Third, we do not have information about infection with the SARS-Cov-2 virus since testing was not widely available at the time and the vast majority of women were never tested. We therefore cannot separate out direct mortality effects from the indirect effects of the pandemic. Finally, the study was not designed to test for mechanisms so we can only speculate as to underlying causes of infant death.

STUDY RESULTS

We enrolled 36,607 pregnant women from 1,365 communities in the study. 34,299 gave birth between July 2019 and December 2020, 28 died while pregnant, 1,841 had an early pregnancy termination, 190 were never pregnant, 177 were not located at follow-up, and 72 did not give consent for the follow-up. In Table A.3 we report summary baseline characteristics of study participants (22).

Exhibit 1 graphs the probability of a stillbirth and newborn infant death in each month between August 2019 and November 2020. The figure, therefore, shows mortality in the eight months before, and after, the start of the pandemic. We fit flexible local polynomial regressions to the data and plot the resulting estimates and 95% confidence intervals. The data are increasingly sparse towards the end of the time series (see Table A.4 (22)), as most women in the sample have delivered already, so the estimates in the last few months are noisy (the confidence intervals are noticeably wider).

Exhibit 1 (Figure). Monthly Trends in Stillbirths and Newborn Deaths in the 8 Months Before/After the Start of the Pandemic.

Source: The data are from an in-home survey of women enrolled in the study.

Notes: Exhibit 1 graphs the probability of a stillbirth and newborn death, respectively, by month of birth. There are only a few observations in November 2020 so these are combined with October 2020. Variable definitions are in the text. We fit flexible local polynomial regressions to the data using an Epanechnikov kernel. Circles denote monthly averages. Dashed vertical line indicates the start of the pandemic.

Exhibit 1 shows that mortality was essentially flat in the months leading up to the pandemic but, by May, started to increase. The trendlines suggest that, by the end of the period, mortality had started to dip back down (though additional data would be needed to confirm this). For comparison, we graph mortality trends in the comparator period (2014–2018) in Exhibit 2. We calculate average mortality in each month and examine whether there is any evidence of an increase in mortality between April and November in the comparator period. We find no such evidence: the probability of an early infant death is pretty stable throughout the year. In the Appendix (22), we plot mortality trends between 2014 and 2018, separately for December-March births and April-November births, to show that they proceed on parallel tracks in the pre (comparator) period, suggesting that December-March births provide a good counterfactual for April-November births.

Exhibit 2 (Figure). Monthly Trends in Stillbirths and Newborn Deaths in the Five Years Prior to Enrollment.

Source: The data are from an in-home survey of women enrolled in the study.

Notes: Exhibit 2 graphs the probability of a stillbirth and newborn death, respectively, by month of birth in the five years prior to enrollment (data is aggregated by calendar month of birth). Variable definitions are in the text. We fit flexible local polynomial regressions to the data using an Epanechnikov kernel. Circles denote monthly averages. Dashed vertical line indicates the start month of the pandemic in 2020. There were 31,532 births between December 2013 and November 2018.

There is a level increase in mortality between the comparator and treated periods, suggestive of under-reporting of mortality for prior births. This, however, should not trouble the double-difference estimator provided that reporting error, such as it is, does not systematically vary by season of birth. Additional discussion is provided in the Appendix (22).

Exhibit 3 is a 2 × 2 table comparing mortality in the exposed/unexposed groups in the treated/comparator periods. The table reported the number of children born and the number of deaths in each cell. We see that the unadjusted probability of a stillbirth increased by 1.37 percentage-points in the treated period, from 5.2% to 6.5% (P <.001). This compares to a change of −0.17 percentage-points over the same period in prior years (P =.385). We also see an increase in newborn deaths in the treated period. The unadjusted probability of a newborn death increased by 0.84 percentage-points, from 3.2% to 4.0% (P =.009). This compares to a change of −0.1 percentage-points over the same period in prior years, from 1.3% to 1.2% (P =.471).

Exhibit 3 (Table). Rates of Stillbirths and Newborn Deaths Among Births in the Treated and Comparator Periods.

Source: The data are from an in-home survey of women enrolled in the study.

		Stillbirths		Newborn deaths
		Comparator period	Treated period	Comparator period	Treated period
		2014–2018	2020	2014–2018	2020
Unexposed births	Number of deaths	238	822	134	477
(December-March)	Number of births	10751	15931	10513	15109
	Percent	2.2%	5.2%	1.3%	3.2%
Exposed births	Number of deaths	425	465	239	266
(April-November)	Number of births	20781	7119	20356	6654
	Percent	2.0%	6.5%	1.2%	4.0%
Change		−0.17%	+1.37%	−0.1%	+0.84%
[95% CI]		[0.55 to 0.21%]	[0.64 to 2.1%]	[−0.38 to 0.17%]	[0.21 to 1.47%]
P-value		.385	<.001	.471	.009

Notes: Variable definitions are in the text. The change is the difference in mortality rates between exposed and unexposed births in each period. CI denotes confidence interval.

The results from the linear probability model are reported in Exhibit 4. We report an unadjusted specification (Column 1) and a covariate-adjusted specification (Column 2). Both are similar. The covariate-adjusted model indicates that the pandemic was associated with a 1.1 percentage-point increase in stillbirths (a 22% relative increase) and a 0.72 percentage-point increase in newborn deaths (a 23% relative increase).

Exhibit 4 (Table). Association between the COVID-19 Pandemic and Early Infant Deaths: Regression Model Estimates.

Source: The data are from an in-home survey of women enrolled in the study.

	Stillbirths		Newborn deaths
	(1)	(2)	(3)	(4)
Estimate	0.0110***	0.0114***	0.0071**	0.0072**
	(0.0041)	(0.0039)	(0.0034)	(0.0035)
Controls	No	Yes	No	Yes
Observations	54582	54580	52632	52630
Mean of dependent variable	0.0516	0.0516	0.0316	0.0316

Notes: The dependent variables are in the table header. Variable definitions are in the text. Model estimates are from a linear probability model of the outcome on the interaction between the exposure indicator and the treated/comparator period indicator. The unadjusted model includes state, year and calendar month-of-birth fixed effects. The adjusted model includes the following covariates: child’s sex, mother’s age, ethnicity, religion, education, and household wealth quintiles, and also controls for any interventions in the community. Standard errors in parentheses.

^∗∗p < 0.05

^∗∗∗p < 0.01.

To put this into context, we translate it into number of infant deaths. Scaling our estimates by the projected number of births in these four states between April and November 2020 (assuming a crude birth rate of 38 per 1,000 people) we calculate an additional 13,000 infant deaths that are attributable to the Covid-19 pandemic. For further context, we note that this is in the four states included in the study; Nigeria has 36 states and one Federal Capital Territory.

Sensitivity checks

We carried out multiple sensitivity checks that are reported in the Appendix (22). First, we dropped one comparator year at a time, to ensure that the results were not driven by one particular year. All the resulting estimates are similar to the main specification (Figure A.3). Next, we carried out a falsification test: Using only data for prior years, we iteratively assigned the ‘treatment’ to each year, using the other years as a comparator, and re-estimated the difference-in-difference model. We should not see any increase in mortality in these placebo models. We do not (Figure A.4). We also checked sensitivity to alternative model specifications. Across all specifications, the estimates look very similar to the main specification (Table A.5). In Table A.6 we examine whether the study interventions may have modified the effect of the pandemic. The results are suggestive of a smaller mortality effect among women who received an intervention but none of the coefficients are statistically significant, and a joint test that all the interaction terms are equal to zero yields p-values of 0.37 and 0.23 for stillbirths and newborn deaths respectively.

Additional analysis

A natural question is: what explains this increase in mortality? Our data are not well-suited to answering this question but we can, at least in broad strokes, examine some leading hypotheses. One leading explanation for the increase in infant deaths is that the pandemic deterred women from seeking health care. In Figure A.6 we find no evidence of a decrease in health care utilization. Another possibility is that while utilization levels, on average, did not reduce, the pandemic may have led to changes in where care was provided. For example, women might have substituted away from higher quality settings such as general hospitals (e.g., because of a higher perceived risk of contracting the virus) to lower quality settings. We find no evidence of this in Figure A.7.

Another possibility is that the increase in mortality is related to preterm deliveries. If the pandemic led to more preterm births for example — though existing evidence on this front is contradictory (8,12,26) — this could help explain the increase in neonatal deaths. While we do not have data on precise gestational age at birth, we asked women at endline if they gave birth at, before, or later than the expected time. Earlier-than-expected births serve as a useful proxy for premature births. We do not find persuasive evidence of a change in the probability of a preterm birth (Figure A.8). In the next section, we discuss other possible explanations for the increase in mortality.

DISCUSSION

This paper has examined an important policy question: whether the COVID-19 pandemic has led to an increase in infant deaths. Using a quasi-experimental difference-in-difference strategy and data on birth outcomes for a large cohort of pregnant women in Nigeria who took part in a prospective study, we found that stillbirths and newborn infant deaths have significantly increased during the pandemic.

This study adds to existing evidence regarding the effect of the COVID-19 pandemic on child outcomes (8,12). The closest related study is KC et al.(8) which examined institutional stillbirth and neonatal mortality rates in nine hospitals in Nepal. They estimated that institutional stillbirth rates increased by about 50% (from 14 per 1,000 to 21 per 1,000) during COVID-19 lockdowns, while institutional neonatal mortality tripled (from 13 per 1,000 to 40 per 1,000). As we have noted, attempting to infer the effects of the pandemic using hospital births is problematic in a context where a large number of births take place outside health facilities—in Nepal 40% of births take place in non-institutional settings (27). Further complicating issues, the composition of hospital users, itself, likely changed in response to the pandemic (20,28). This is likely to lead to an over-estimate. A key strength of this study is that our sample includes all births, regardless of location. This allows us to draw more general (and generalizable) conclusions. Our data also covers a much longer period encompassing the entire first wave of the pandemic.

Our data is not well-suited for examining mechanisms but we do not find evidence that the increase in mortality is a result of women being less likely to use health care services during the pandemic (29) or substitution from higher to lower-quality care settings. The increase in mortality could be related to delays in seeking care, or delays in receiving appropriate care because of disruptions to care provision during the pandemic (30). Pandemic effects on delivery of health care, in particular, provide a plausible pathway. Okeke (31), for example, finds evidence of risk avoidance behavior, in this setting, by health workers during the pandemic. Health workers took actions to reduce their risk of getting infected, e.g., moving patient consultations outside and refusing care to patients with Covid-19 symptoms. These actions not only reduced access to care but, predictably, led to worse care. Using data from direct observations of provider-patient interactions in outpatient care settings, Okeke (31) finds that health workers were substantially less likely to carry out clinical procedures, such as physical examinations, that required physical contact with patients. While this is a plausible pathway, we are extremely cautious about attribution; it is likely that there are multiple contributory factors. Additional research to better understand mechanisms and pathways is needed.

Policy Implications

One implication of our findings is that we may be vastly underestimating the mortality effects of COVID-19. Commentators have noted that low and middle-income countries, like Nigeria, have experienced a relatively low number of COVID-19 deaths, but our findings indicate that there are many more deaths attributable to the pandemic that are not being counted. Counts of COVID-19 deaths may, thus, represent only the tip of the spear. This has major policy implications, especially as the pandemic remains ongoing. If these findings generalize to other low and middle-income countries, they may indicate that the hard won gains in child survival made over the last two decades are at risk of being reversed amidst the ongoing pandemic.

What should policymakers do? First, step up support to frontline health care facilities and workers. Policies to help health care workers reduce their risk such as provision of high quality protective equipment, perhaps coupled with complementary strategies such as ‘danger pay’ to compensate them for the higher risk associated with delivering care during a health pandemic, could help to alleviate negative effects of the pandemic on service delivery. Stepping up efforts to vaccinate health workers will also help. Second, provide additional support to vulnerable groups such as households with pregnant women. One form that this might take is temporary unconditional payments to vulnerable households to help them cope with the effects of the pandemic. Cash is fungible and can be deployed by households to meet various needs, e.g., to buffer the effects of income shocks, to offset higher costs of using health services during a pandemic, or to seek care from higher quality, but also higher-cost, institutions. Such emergency payments can be discontinued after the public health emergency ends (or when alternative policy benchmarks are achieved). It is likely that the benefits of such a program would exceed the costs.

Conclusion

This paper finds that early infant deaths in four states in Nigeria have significantly increased during the COVID-19 pandemic, highlighting the hidden mortality costs of the COVID-19 pandemic. In poorer countries with weak health systems, the additional stress imposed by the pandemic may lead to additional collateral deaths that are not being counted. Our findings suggest that these indirect deaths may outnumber direct deaths from COVID-19. Finding ways to mitigate these effects will be critical. Policies addressing supply-side effects of the pandemic and providing support to vulnerable groups and specifically households with pregnant women will be important. As the pandemic continues it will be important to continue to evaluate these outcomes.