Publication Date

April 1, 1988

Perspectives Section



Research Methods, Women, Gender, & Sexuality

Women’s history has made vast advances in the past twenty years. Where we are going with these advances, however, is less certain and where we should be going is something we might do well to consider, even if we have no expectation that we can agree on one goal.

We can agree, to begin with, that traditional history obscured, neglected, and distorted the historical record and experience of half the world’s population. Since the existence of academic professional history, which is not even 200 years old, this distortion and omission has become institutionalized. Consequently, it has become more difficult to dislodge or to correct the distortions than it was earlier, when next to official history there existed a live and active oral tradition.

The interpretations of primary and secondary literature, which we call history, must always rest on a solid basis of monographic studies. Academic historians in the United States have for over 100 years provided this basis for the history of men and male activities. Historians concerned with documenting and interpreting the history of women have worked for only the last twenty years to try and lay the documentary and interpretive foundation upon which later historiography can build. We must recognize at the outset that we have barely begun our work.

The past twenty years have seen enormous advances in making important primary records accessible—such as the Women’s History Sources Survey; numerous specialized bibliographies; increased numbers of primary source reprint series; increasingly organized and indexed archival sources making topics pertaining to women more easily accessible; and such massive works as Notable American Women.

We have begun the study of demographic, legal, and governmental sources and have, sporadically and unevenly, studied community records to reconstruct the lives and experiences of women. Thus, we know a good deal about Lowell, Massachusetts; Utica, New York; and Petersburg, Virginia, in the antebellum period, and we have freely generalized from these excellent studies. But do they really tell us what we need to know about the lives of most women in most regions of the United States in that period?

We have studied some women’s organizations rather fully and quite neglected others. I am not certain that such research decisions were made on the basis of the availability of sources, for at times vast and readily available sources have been ignored while obscure and difficult sources have been studied. Finally, in terms of reconstructing the female experience and letting the female voice be heard directly in the interpretation of autobiographical sources, we should look at biographical works and the reinterpretations of certain major and minor historical figures. Here, too, we find a strangely skewed list of priorities, which I find difficult to explain.

Based on my experience in a number of searches in women’s history in the past three years, I can testify to the fact that the research interests of available candidates show the same peculiar clustering of interest. There is a predominance of people working in twentieth-century women’s history, followed by those in the Progressive period, with the smallest number working in colonial history. We find that more work is being done in periods that have already been mined and explored by others than in those periods where there is the greatest dearth of work. Another way of putting it is that we are training specialists in women’s history—or they are choosing to train themselves—in inverse ratio to the existing needs of the field. I have long been puzzled by this observation and have tried to understand its causes. This induced me to attempt to document my impressionistic observations and look at the ways in which American women’s history developed.

The figures that follow (see Table I) are based on my selected Bibliography in the History of American Women, which I revised in 1986. While I am sure there are some regrettable omissions, I included in it the books reviewed in the major relevant journals and those most frequently cited and used in teaching. Therefore, these figures, while not definitive, give a rough overview.


Table I: Books on American Women's History Published

YearNumber of Books


In 1960 anyone interested in studying American women’s history could draw on thirteen books, of which five dealt with colonial women, three with Southern women, and only one book, Flexner’s, attempted a general overview of the field. Between 1960–70, eleven new book titles were added to this list. By 1970 there were four historians in the academy who defined themselves as specialists in women’s history (Anne Firor Scott, Janet James, A. Elizabeth Taylor, and ) and several others who had done one book, but whose major interests were in other fields and subjects (Carl Degler, Clarke Chambers, Keith Melder, Aileen Kraditor, Allen Davis).

Ten more new titles were added between 1970–75. Thus, the fifteen-year period between 1960–75 produced twenty-one titles in women’s history. Not a single one of the authors of all the titles published before 1975 had specialized in women’s history in his or her training, since no such specialization existed on the graduate level. All the work produced before 1975 was produced by self-trained specialists, who, insofar as their books were the products of dissertations, worked under the direction of mentors who were themselves untrained in this specialization. The group publishing between 1960–75 included ten men and seven women (several of whom authored several books during this period). The figures do not include biographies and works on racial minorities, with which I will deal separately.

The real take-off for the field is indicated by the publishing figures for the five-year period 1975–80, in which thirty-six books on women’s history were published. Only eight men are among the authors; among the female authors I can identify only three as being above the age of fifty. The women authors in this group are the young women who came out of the women’s movement, yet, by and large, their training was still under male mentors. l can identify only two among them who were trained by women who themselves specialized in women’s history. I believe these sociological factors have something to do with the kind of research topics the authors selected and with the questions they asked. Many of the topics focus on questions coming out of the twentieth-century women’s movement-the importance of sexuality and reproduction in the lives of women; the struggles of working women; a reinterpretation of the women’s suffrage movement and of the modern women’s movement. Several of these books do the kind of monographic work designed to reconstitute the female experience in colonial America and in the nineteenth century; several deal with questions of women and religion; and only one, the work of a sociologist, Elise Boulding’s massive The Underside of History, attempts a general theoretical and empirical overview.

When we come to the period 1981 to the beginning of 1987, we find an explosion of scholarship. At least forty titles are published in this period, many of these authored by younger women who studied under female mentors and who received a sound grounding in women’s history during their training years. Much exciting and important work emerged from this group, many of whose members are still in their early thirties and thus have their best work ahead of them. This promises well for the future.

From Table II it is easy to see that more than two-thirds of all books in women’s history are written about the past 100 years and more than one third deal with the post-1920s period. As things currently stand, the short expanse of the history of U.S. women is very unevenly covered. There is virtually no work on the first 100 years prior to 1720 and very little work in the period to 1800. The coverage of issues and events in the antebellum period is woefully inadequate, with work on Southern women showing even less advance than that on Northern women. What are we to make of the five volumes produced on women in Civil War and Reconstruction, four of them written before 1970, one before 1975, and only one in 1980 (Dannett, Massey, Swint, Wiley, and J. Jones)? Can anyone really maintain that the lives and experiences of women in this crucial period of U.S. history are less interesting or less significant than the heavily mined decades after 1920? With literally hundreds of women’s diaries, autobiographies, and correspondence available for the Civil War and Reconstruction period, one cannot explain this dearth of scholarship as due to a shortage of primary sources.

Table II: Topial Breakdown of 291 Titles in U.S. Women's History

TopicsNumber of Books
Civil War5


Another fact obvious to anyone who has taught American women’s history in chronological sequence, is the absence of any narrative synthesis or monographic work for the years 1840–80. After we leave the Lowell mill girls, we seem unable to pick up the threads until we focus on the 1876 Temperance Crusade, the women’s clubs, and the later phases of the suffrage movement. The only available works dealing with this period tell us about the westward movement of women. Yet American women worked in homes and factories, attempted to organize unions, were part of the National Labor Union and the Knights of Labor, and worked in the Granger movement and Greenback Party. Why are their activities less attractive to young scholars than those of the twentieth- century generations?

Let us take a look at more recent scholarship represented by dissertations registered between 1980 and early 1987. These dissertations will form the scholarly basis for the major publications in the next five years. With the help of my project assistant Elizabeth Williams, I have analyzed the 312 dissertations listed in the AHA’s Doctoral Dissertations in History for this period. I was amazed at the number of women’s history dissertations registered, which certainly speaks to the growth and dynamics of the field. It is also interesting to note that these dlissertations issue from thirty-two institutions, with nineteen institutions producing 50 percent of all dissertations. Considering that the number of graduate programs in women’s history is small and relatively recent, so that most of them are not yet represented among the dissertation producers, you may be interested to know that nine institutions produced more than seven dissertations each. They are a rather surprising lot: Yale, thirteen; Columbia, ten; Boston University, Harvard, and Stanford, nine each; Ohio State, Rutgers, and SUNY-Binghamton eight each; and New York University, seven.

Taking the distribution by period (see Table III), if we deduct the fourteen dissertations in the miscellaneous category, making the total 298, we find nearly two-thirds of the work in the twentieth century and the Progressive period and only 6 percent in the period before 1820. There is, however, a very encouraging increase in work on the nineteenth century.

Table III: Analysis of 312 Women's History Dissertations 1980–87

TopicNumber of Books
Antebellum & General 19th Century100
Civil War8
Progressive Period64


As to topical interest, there is a slight shift: biography, which was very poorly represented in the earlier work, now accounts for forty-eight dissertations. Labor and work accounts for forty-seven dissertations, with education and cultural topics next in line, forty and thirty-two. Social history topics, religion, and medical topics are next, fifteen, twenty-one, fourteen with suffrage history, modern feminism, and organizations next in popularity, nineteen, nineteen, thirteen. The remaining topics are family/motherhood; sex/gender; frontier/rural; military/peace/legal; and intellectual. Immigrants and slavery/abolition account for less than ten dissertations in seven years. Civil War and Reconstruction remain as unpopular as ever, and two of the three dissertations on that topic deal with black slave women.

Another unpopular topic (in reverse proportion to its immense significance for the history of women) is housework, with only one dissertation on the subject. If we had hoped to find a broader base of community studies emerging for the next generation, we were disappointed—there were only two. While twenty-five dissertations in all periods deal with subjects pertaining to racial minorities, only three of these are comparative, which seems to me a distinct shortcoming. ln general, comparative history accounts for only seven dissertations, although this methodology has seemed for some time to be among the most promising for this field.

The single most popular subject in women’s history is easily identified; it is female clerical workers. Six new dissertations will be added to the two books published earlier on this subject. In fact, each of these has something new and interesting to add to the study of this major female occupation, but the cluster of work here only highlights the thinness of work in other, equally important fields. Since I’m omitting work under way that is not based on a dissertation, i.e., second and third books, this analysis is impressionistic.

Finally, let me discuss biographies. In my 1986 bibliography the persons most popular with biographers were Margaret Fuller (eleven biographies printed before 1978); Eleanor Roosevelt (eight before 1984); Margaret Sanger (four before 1979); Emma Goldman (five biographies, of which three are since 1984); and Frances Wright (three before 1984). Following the principle observed above—that historical work will be done in reverse ratio to need—we find among new dissertations four more on Margaret Fuller and two on Frances Wright. Between 1980–87 several major figures had biographies done on them: Abigail Adams (three since 1980); Jane Addams (two); Carrie Chapman Catt; Abigail Duniway; Elizabeth Cady Stanton (two since 1980, with a new dissertation waiting to be published); and Frances Willard. It is encouraging to note that the number of biography dissertations is sharply increasing.

Yet, the list of great women who are due for modern biographical treatment remains large. Susan B. Anthony has not had a biography since 1973, with the last several biographies heavily influenced by a Freudian conceptual framework. There is no question of available source material here, nor of need and reader interest. Dorothea Dix, one of the most important U.S. reformers of the nineteenth century, is memorialized in a 1971 biography that does not do justice to her significance. The situation is similar for Lucretia Mott with two biographies in the twentieth century, the latest in 1971. Lucy Stone continues to suffer the neglect imposed upon her by the partisanship of the Stanton-Anthony wing of the suffrage movement. The one and only modern biography on her is dated 1961. On both of these great leaders of the suffrage movement, there are vast available sources. In the Progressive period, Lillian Wald awaits a good modern biography.

The story is totally dismal for the great black women leaders of the nineteenth and twentieth centuries. The following have not bad biographies written about thenn: Charlotte Forten, Frances Harper, Anna Cooper, Mary McCleod Bethune, and Ida B. Wells. Fortunately, there is among the new dissertations one on Mary Church Terrell and another one on the black sculptor Meta Fuller, but otherwise the forty-eight new biographical dissertations continue to neglect women of other than white race, which is evident in the earlier historiography.

Feminist scholarship in psychology, literature, and anthropology has developed new methodological tools that could and should be used to make women of the past come to life in a new way that is meaningful for contemporaries. The first wave of feminism produced hagiographic biographies in which the living human beings were subordinated to their public images. New feminist biographies could break out of this division of the public and the private; they could and should address the ways in which women’s lives and work intersect differently than do those of men. They might explore mother-daughter relationships and use life-cycle analysis to understand the patterns of women’s lives. A feminist analysis would look at the support systems women constructed for their activities and at the familial and female friendship networks that sustained women’s public activities. We need also to analyze more fully and with the tools of modern feminist scholarship the mental product of women’s lives, their ideas, their writings, and their discourse. The biographical field within women’s history remains one of the most promising and challenging for the researcher.

Having surveyed the trends of past and upcoming scholarship, let me discuss briefly what I think the challenges and priorities should be. These fall into four categories: 1) Restoring and documenting the female past; 2) Interpreting the female past from the female point of view, which implies a redefinition of the values by which we make historical judgments; 3) Treating women as the majority, which means making differences and comparisons the core of our analysis; and 4) Creating a new conceptual framework by which to deal with the history of women and men.

Please notice that l left out mainstreaming women’s history. That is because l consider that endeavor premature in every way. Until we have established the monographic base on which, for most periods of American history, a fair comparison between male and female activities is possible, we cannot incorporate women into the traditional narrative without subsuming them. In fact, we probably can never do this until we are ready to change the paradigm by which we tell the stories of the past for both sexes.

Having discussed restoring and documenting the female past, the second task, to interpret the female past from the female point of view, demands not only that we elicit the voices of women from the primary record but learn how to listen to them. It demands also that we question and redefine the values by which we order historical data. Traditional, male-centered history has focused on public actions and power as central concerns. These have affected periodization-wars, presidential elections, or major economic changes are the markers by which we periodize. In interpreting the female past we need to focus on the activities of women and upgrade their value as topics of historical scholarship. To this day we do not have a history of child care. The vast and varied local efforts by which women built the infrastructures of communities, their institution-building, their multiple innovations for social welfare, and their impact on public decision long before the winning of suffrage, form a story as yet incompletely documented and incoherently told.

Women introduced kindergartens in this country and institutionalized them in community after community-another untold story. Women’s cultural activities, the founding of reading circles, libraries, centers for art and music, their support of theaters, museums, and orchestras need to be seen not as isolated efforts, but as coherent and consistent endeavors spanning centuries. As we study women’s social and welfare activities, we need to begin to link the various case studies and see if we can find the larger patterns. Such larger patterns would show us the ways in which women acted differently from men as agents in history.

The third point, treating women as a majority, is much more difficult to implement than are the first two. It means that our awareness of differences among women must permeate all our thinking. No one expects that it is possible to make any valid generalization about about men, and yet that is constantly done when thinking about women. The particulars of region, religion, ethnicity, and race are the ground on which we must test every generalization we make. We still write about the nineteenth-century mass movements as though they were unified or homogenous, when in fact they were complex coalitions of often contradictory interests. We search for sisterhood in definitional unity, when in fact sisterhood takes many specific forms and contains many tensions. Making differences the core of our analysis may lead us to do more work comparatively, which might be very useful. For example, a comparison of the social welfare organizing of white and black women could tell us more about either group than could separate studies. Comparing women of different classes in a given time and place could help us to see how gender affects class formation. Some very promising work has already been done on the intersection of race, class, and gender, but there are still vast blank spaces to be filled.

On the subject of differences, some very promising work is now under way to restore the experiences of twentieth-century lesbians and their communities in the historical record. l know of no work now under way that reaches back to the nineteenth century to reconstruct the lesbian past. Has Carroll Smith-Rosenberg really said the first and last word on the subject of homoerotic relationships? I believe the time has come for testing out her theoretical insights in other primary sources. I have called elsewhere for a different and more sophisticated approach to the many women whom we know as leaders in the nineteenth century and whose private lives were spent with one or more women in long-lasting relationships. We need to deal with such relationships as central, not tangential aspects of these women’s private and public lives, and we need to know how they viewed these relationshlips, and how others of their time viewed them. Another approach to lesbian history is to study changing definitions of deviance in an economic and comparative context, looking at the function of such definitions in the maintenance of sexual norms. When and why did the strong-minded spinster of the nineteenth century become the lesbian? How and when did the self-definitions of lesbian women change? We may know the answers in a few instances, but we do not know the answers in a larger context. These comments are not intended to define this new and important field, but rather to encourage a broader, more comprehensive view of it, and one not necessarily confined to lesbian historians.

As to the fourth question—the new paradigm by which to order the history of women and men-we have not advanced very far toward answering it. In surveying the past literature and the recent dissertations, I was struck by the virtual absence of theoretical work. Feminist theory seems to have developed out of many other disciplines, and historians, by and large, have been content to try out these methodologies and theories instead of developing their own, with mixed results. Social theory, literary and linguistics theories, anthropological concepts, and psychological theories all have appeared in the works of feminist historians, while the reverse has not been the case. In fact, much of feminist theory suffers from ahistoricity and from a lack of context. And yet, there is in history a strong tradition of historical theory being used as an explanatory framework-for example, in the work of Condorcet, Hegel, Marx and Engels, Durkheim, and Habermas, to name just a few. Current feminist work in literature, and especially in the field of theology and religious studies, has advanced much further than we have in challenging the basic paradigm of the discipline and in trying to construct a new, more truly universal paradigm.

We could, to begin with, challenge the ahistoricity of some influential theories, like those of Simone De Beauvoir, of the structuralists and post-structuralists, and those theories which construct psychology without regard to its social context. We might ask some basic transforming questions of our empirical research: How does the concrete social situation differ for men and women at any given time, and how does that difference affect the outcomes? What is the tension between reality and myth in women’s lives, and how has it affected women’s consciousness? What is the relationship between changing gender definitions and changing economic and social conditions? What are the points of change in women’s historic experience by which we might periodize the history of women? If women were at the center of our analysis regarding any period or any series of events, how would our account and analysis be changed?

This last is, of course, the crucial, transforming question because it rests upon the centrality of women to events. For the past twenty years we have cleared a small space for ourselves; we have opened up a window or several windows on women’s past; we have restored some lost voices and documented some distorted or forgotten events. But until we redefine the paradigm and find the true relationship between female and male actors as agents in history, we will not have succeeded. The past twenty years have been exciting, challenging, at times exhilarating. The next generation of historians of women will be creating its own tools of analysis, and bring us forward toward building a sounder foundation and a more solid and truly representative structure of historical knowledge.

Gerda Lerner is Robinson-Edwards Professor of History at the University of Wisconsin–Madison. This article is based on a paper she gave at the AHA annual meeting in 1987.