Cameron Peng 教授分享行为金融学领域创作心得 Cameron Peng on Doing Research in Behavioral Finance
本文于 2026 年 7 月 23 日同日发布于微信公众号 Impactful Research 与本网站。
Published on 2026-07-23 on both the WeChat official account Impactful Research and this website.
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这个公众号的第二十八篇文章，我们很荣幸邀请到伦敦政治经济学院的彭程教授分享他在行为金融学（Behavioral finance）领域的创作心得。
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Q1：在行为金融学领域，我们可以观察到一种很有意思的现象：一方面，正如你之前提出的“偏差合集（bias zoo）”，很多研究试图将各种行为偏差进行系统梳理与整合；另一方面又倾向于对某一种单一偏差进行深入挖掘。你如何看待这一发展趋势？在你自己的研究中，又会如何进行取舍——是关注多个行为偏差之间的关系，还是聚焦于某一个特定偏差进行深入研究？
In the field of behavioral finance, we can observe an interesting phenomenon. On the one hand, as you previously pointed out with the idea of the “bias zoo,” a growing body of research has attempted to systematically organize and integrate the wide range of behavioral biases that have been documented. On the other hand, many studies have increasingly focused on examining a single bias in depth and exploring its underlying mechanism. How do you view this trend in the development of the field? In your own research, how do you approach this trade-off? Do you focus more on understanding the relationships among different behavioral biases, or do you prefer to concentrate on one specific bias and investigate it in greater depth?
我认为，这其实是科学研究中一个非常自然的发展过程，有点类似于经济学中的繁荣与萧条周期。当一个新的现象出现时，为了解释这一现象，研究者往往会提出大量不同的理论解释。这一阶段本质上是在不断拓展研究边界，虽然解释路径多样、观点创新，但这本身是一件积极的事情。然而，当解释框架不断累积、复杂性达到一定程度后，研究领域往往会进入一个收敛与整合的阶段。科学研究的推进过程，实际上就是在“拓展”与“整合”的交替过程中不断螺旋式上升。
I think this is actually a very natural process in the development of science. In some ways, it resembles the boom-and-bust cycles we observe in economics. When a new phenomenon emerges, researchers often propose a wide range of theoretical explanations in an attempt to understand it. This stage is essentially about expanding the frontier of knowledge. Although the explanations may differ and many ideas may be exploratory, this diversity is a positive force for scientific progress. However, as theoretical frameworks continue to accumulate and the complexity of the field reaches a certain point, research often moves into a stage of convergence and integration. In my view, the advancement of science is ultimately driven by a continuous cycle between expansion and consolidation, through which knowledge evolves in a gradual, upward spiral.
例如，在行为金融学发展的早期阶段，我们认为投资者会做出大量非理性决策，并表现出各种系统性的错误行为。围绕这一核心观点，很快形成了大量研究。一些研究认为，这些现象源于投资者非理性的偏好；另一些研究则强调，问题来自投资者信念形成过程中的偏差；还有一些研究关注市场摩擦等制度性因素。当这些不同解释逐渐提出后，研究领域便产生了新的需求：是否能够建立一个更加简洁的理论框架，以更经济的方式解释这些现象？也就是说，能否通过更少的假设获得更强的解释力。这也正是你刚才提到的，对某一具体机制进行深入研究，并考察其能够解释多少现象。与此同时，我们还需要进一步思考：某一种理论解释究竟能够覆盖多大的范围？而这一问题最终又需要通过实证研究来回答。因此，我认为，“拓展”与“整合”实际上对应了理论研究与实证研究中的一种自然演进过程。实证研究不断发现新的现象，从而推动新的理论解释产生；理论研究则进一步拓展这些解释，探索其适用范围和解释能力；随后，实证研究又会继续检验这些理论的边界。 整个过程实际上是在循环往复中不断推进。
For example, in the early development of behavioral finance, researchers began with the observation that investors often make irrational decisions and exhibit systematic patterns of mistakes. Around this central idea, a large body of research quickly emerged. Some studies argued that these behaviors were driven by investors’ irrational preferences; others emphasized that the underlying issue was biased belief formation; while another line of research focused on institutional factors, such as market frictions. As these different explanations accumulated, the field naturally began to face a new question: could we develop a more parsimonious theoretical framework that explains these phenomena in a more efficient way? In other words, can we achieve greater explanatory power with fewer assumptions? This is closely related to what you mentioned earlier—the effort to examine a specific mechanism in depth and understand how much of the observed behavior it can explain. At the same time, we also need to ask a broader question: how far can a particular theoretical explanation actually extend? What range of phenomena can it account for? Ultimately, these questions need to be answered through empirical research. Therefore, I think the process of “expansion” and “integration” reflects a natural evolution in both theoretical and empirical research. Empirical studies continue to uncover new patterns and motivate the development of new theories. Theoretical work then expends these explanations, exploring their scope and explanatory power. Empirical research subsequently returns to test the boundaries of these theories. The entire process is an ongoing cycle through which scientific knowledge continues to advance.
如果回到行为金融学的发展历程，也可以回应你最初提出的问题。以行为金融学的发展为例，20世纪90年代末，该领域刚开始兴起时，市场中出现了大量传统理论难以解释的异常现象，例如动量效应（momentum）、价值效应（value）等。进入2000年前后，外推偏差（extrapolation）、过度自信（overconfidence）以及前景理论（prospect theory）等核心概念逐渐确立。随后十余年间，研究者主要围绕这些机制展开大量实证检验，探讨它们究竟能够解释多少市场现象。
If we look back at the development of behavioral finance, it also provides a good illustration of the question you raised earlier. In the late 1990s, when the field was still emerging, researchers began to document a wide range of market anomalies that were difficult to explain within traditional frameworks, such as momentum and value effects. Around the early 2000s, several key concepts gradually became central to the field, including extrapolation bias, overconfidence, and prospect theory. Over the following decade or so, researchers primarily focused on empirically testing these mechanisms and examining the extent to which they could explain different market phenomena.
随着研究不断深入，一些批评和反思也逐渐出现。例如，有学者开始质疑行为偏差的数量是否过多，以及研究过程中是否存在过高的研究自由度。这些讨论进一步推动了研究者对已有成果进行整合和重新审视。目前来看，行为金融学框架中的核心内容已经相对明确。在偏好层面，最具代表性的理论是前景理论对非标准偏好的刻画；在信念层面，外推偏差所描述的信念形成机制是最经典的理论之一；此外，围绕过度自信也形成了一系列重要理论。
As the field continued to mature, it also attracted increasing scrutiny. Some scholars began to question whether behavioral finance had accumulated too many biases and whether researchers had too much flexibility in identifying and interpreting them. These debates, in turn, prompted the field to step back, reassess its existing findings, and search for a more unified framework. Looking at the field today, its core building blocks have become much clearer. On the preference side, prospect theory remains the leading framework for understanding non-standard preferences. On the belief side, extrapolation has emerged as one of the canonical models of belief formation. At the same time, a rich body of work has developed around overconfidence, establishing it as another central pillar of behavioral finance.
近年来，在行为金融领域的学术讨论中，一些研究者开始提出新的问题：在已有“偏好”和“信念”两个核心框架的基础上，是否可以进一步引入更深层次的心理学微观基础？这也催生了一些新的研究方向，例如探讨偏好和信念的形成机制，以及如何对这些过程进行更加细致的微观刻画。因此，我认为当前行为金融学实际上又进入了一个新的“拓展—整合”阶段。一方面，研究者正在不断探索新的微观基础，提出更多可能的理论机制；另一方面，也需要思考如何将这些新的微观基础纳入更加统一的理论框架。 从这个意义上说，当前行为金融研究正处于新一轮可能性拓展阶段，而未来也必然会出现更多围绕理论整合的研究努力。
More recently, the conversation has started to shift once again. Building on the two established pillars of behavioral finance—preferences and beliefs—researchers have begun asking whether these frameworks can be grounded in deeper psychological microfoundations. This has opened up a new wave of research aimed at understanding not only what people believe or prefer, but also how those beliefs and preferences are formed in the first place, and how these processes can be characterized at a much finer level of detail. In that sense, I think behavioral finance has entered another cycle of expansion and integration. On the one hand, researchers are continuing to explore new psychological microfoundations and propose new mechanisms of behavior. On the other hand, there is an equally important effort to bring these emerging ideas together within a more unified theoretical framework. So, in my view, the field is once again in an expansionary phase, with many new possibilities being explored. Over time, however, I expect another wave of work to focus on synthesizing these ideas into a more coherent body of theory.
Q2：顺着这一学术前沿进一步追问，如果我们从“信念”和“偏好”继续向下拆解其微观基础，那么在当前是否已经出现了某一种具有明显优势、并展现出更强解释力的底层理论框架？还是说，目前这一领域仍处于不断探索和提出新可能性的阶段？也就是说，研究者正在尝试从不同角度寻找行为背后的微观机制，但对于哪一种理论框架能够提供更强的解释力、是否会在未来成为主流，目前可能还需要更多理论发展和实证证据来进一步检验？
Following this line of research, I would like to ask a further question. If we continue to unpack the microfoundations underlying “beliefs” and “preferences” has the emerging field identified any particular theoretical framework that appears to have a clear advantage and offers stronger explanatory power? Or is the field still at a stage where researchers are actively exploring different possibilities and proposing new candidate frameworks? In other words, researchers are currently approaching the micro mechanisms underlying behavior from multiple perspectives. But when it comes to the question of which theoretical framework can ultimately provide the most powerful explanation—and whether one of these approaches will become the dominant framework in the future—we may still need further theoretical development and empirical evidence before reaching a conclusion.
这个问题其实也取决于研究者如何开展自己的研究。
I think the answer also depends on how a researcher approaches the problem.
如果你对某一种信念形成机制已经有较强的经验判断，并且比较清楚这种信念是如何产生的，那么你可能更多关注的是：如何建立一个模型来刻画并检验这一信念形成过程。 比如我们关于投资者记忆的论文（Investor Memory and Biased Beliefs: Evidence from the Field），基本就是从实证观察出发来展开理论叙事的。我们认为，这一理论机制与我们的直觉高度契合，也能够与现实中的经验观察形成呼应：人们在预测未来时，往往会依赖过去的经历和记忆；而信念的形成既可能来源于自身经历，也可能来源于对他人行为或外部信息的观察。
If you already have a strong experience-based judgment about a particular mechanism of belief formation and a fairly clear idea of how those beliefs arise, your focus is likely to be on developing a model that captures that process and testing whether it is supported by the data. Our paper Investor Memory and Biased Beliefs: Evidence from the Field is a good example of this approach. We started with an empirical observation and then built a theoretical narrative around it. We found the proposed mechanism compelling because it aligns closely with both intuition and real-world experience. When people form expectations about the future, they naturally draw on their past experiences and memories. Those beliefs may be shaped by their own experiences, but they can also be influenced by observing the actions of others or by information from the external environment.
因此，我们首先从这些现象中提炼出一个看起来合理的机制，然后寻找已有的理论框架，在此基础上推导出可检验的实证预测，并进一步进行验证。实际上，许多研究者都是以类似方式开展机制研究的。如果希望检验某一种行为机制，这一机制通常首先来源于直觉、内省或对现实现象的观察。 当研究者认为这一机制具有研究价值之后，就会进一步思考：这一机制能够产生哪些具有理论意义的预测？又是否能够找到合适的场景，对这些预测进行有效检验？
From there, we begin by distilling those observations into a mechanism that appears both intuitive and plausible. We then ask whether existing theoretical frameworks can accommodate that mechanism and derive a set of empirically testable predictions. The final step is to take those predictions to the data and see whether they hold. In fact, this is how many researchers study economic mechanisms. A behavioral mechanism often begins with intuition, introspection, or careful observation of the real world. Once a researcher believes that the underlying idea is worth pursuing, the next question becomes: What novel theoretical predictions does this mechanism generate? And just as importantly, can we identify an empirical setting in which those predictions can be credibly tested?
当然，还有另一类研究路径更加偏向实证驱动。例如，我与梁禹澄、樊樵枫合作的那篇论文，最初源于我们发现了一个文献之间的脱节：金融市场中的数据表明，人们往往表现出“过度反应”，但在最经典的信念更新实验中，个体却通常表现为“反应不足”。这种不一致现象非常反直觉，因此我们首先从一个实证问题出发，希望理解这一现象背后的原因。直到获得实证结果之后，我们才进一步回溯并思考其中可能对应的理论机制。所以，我认为这里实际上对应两种不同的研究路径：一种是理论驱动型研究，另一种是实证驱动型研究。
Of course, there is another line of research that is much more empirically driven. For example, the paper I worked on with Yucheng Liang and Tony Q. Fan originated from what we saw as a disconnect in the literature. Evidence from financial markets suggested that people often exhibit overreaction, while in the classic belief-updating experiments, individuals typically appear to underreact. This inconsistency was highly counterintuitive, so we started with an empirical puzzle and tried to understand what could explain this seemingly contradictory pattern. It was only after obtaining the empirical results that we stepped back and considered the theoretical mechanisms that might account for our findings. So, I think there are essentially two distinct approaches to studying mechanisms. One is a theory-driven approach, where researchers start from a theoretical idea or mechanism and then derive testable predictions. The other is an empirically driven approach, where researchers begin with an unexplained pattern in the data and then work backward to identify the underlying mechanism.
回到你刚才的问题，目前许多新一代行为经济学家正在推动一个新的研究方向，通常被称为“认知经济学（cognitive economics）”。如果讨论当前最受关注的微观基础，我认为主要有两个方向：一个是记忆（memory），另一个是注意力（attention）。 记忆与传统行为金融学中的经历效应（experience effect）有着密切联系，并且已经积累了大量实证证据；与此同时，注意力长期以来也是经济学和金融学中的重要研究主题。因此，从已有行为金融学框架进一步向这两个方向拓展，是一个非常自然的发展路径。不过，目前研究者关注的重点已经不仅仅是将这些概念作为模型中的一个“黑箱”机制，而是希望进一步揭示其背后的微观认知过程，将更加接近心理学基础的机制纳入经济模型，并探索这些机制是否能够产生更加精细、具有区分度的理论预测。
Coming back to your earlier question, many researchers in the new generation of behavioral economics are now advancing a new line of research that is often referred to as cognitive economics.If we ask what the most actively studied microfoundations are at this stage, I would highlight two major directions: memory and attention. Memory is closely related to the experience effect that have long been studied in behavioral finance, and there is already a substantial body of empirical evidence documenting its importance. At the same time, attention has also been a central topic in economics and finance for many years. Therefore, extending the existing behavioral finance framework in these two directions represents a very natural progression of the field. However, the current research agenda goes beyond simply incorporating these concepts as “black-box” mechanisms in economic models. Researchers are increasingly interested in uncovering the underlying cognitive processes that generate these behaviors—bringing mechanisms that are closer to psychological foundations into economic models—and examining whether they can generate more nuanced and discriminating theoretical predictions.
事实上，围绕这些主题，目前已经形成了专门的学术交流平台，例如MAC（Memory and Attention Conference）。这也反映出记忆和注意力已经成为当前认知经济学研究中最集中的方向之一。当然，除了记忆和注意力之外，也有许多其他重要的研究路径。例如，一些学者关注信息处理过程中的随机性和偏差，由此发展出“认知噪声（cognitive noise）”等理论。迈克尔·伍德福德关于有效编码（efficient coding）的研究就是其中一个代表性方向。此外，强化学习（reinforcement learning）、复杂性（complexity）等领域的研究，也都试图从更深层次的认知机制出发解释经济行为。
In fact, dedicated academic platforms have already emerged around these topics. For example, the Memory and Attention Conference (MAC) provides a specialized forum for researchers working on these areas. The emergence of such platforms reflects the fact that memory and attention have become two of the most active and influential directions in current cognitive economics research. Of course, memory and attention are not the only important avenues of research. Some scholars have focused on the randomness and biases that arise during information processing, leading to theories such as cognitive noise. Michael Woodford’s work on efficient coding represents one important example of this line of research. In addition, research on reinforcement learning, complexity, and related areas also seeks to explain economic behavior by uncovering deeper cognitive mechanisms.
因此，如果一定要指出目前相对领先的微观基础，我认为记忆和注意力可能是关注度最高、实证积累最丰富的两个方向。但从整体来看，认知经济学仍然处于不断探索和拓展的阶段。未来哪些微观基础能够展现出更强的解释力，并最终发展成为主流理论框架，目前仍然需要更多理论创新和实证证据来进一步检验。
Therefore, if we were to identify the microfoundations that currently appear to be the most developed, I would say that memory and attention are probably the two areas receiving the greatest attention and supported by the richest empirical evidence. However, from a broader perspective, cognitive economics is still very much an evolving field. It remains an open question which microfoundations will ultimately demonstrate the strongest explanatory power and develop into the dominant theoretical frameworks. Answering that question will require further theoretical innovation as well as additional empirical evidence.
Q3：除了理论机制之外，实证层面的测量问题同样非常关键。以信念的度量为例，目前既有问卷调查、实验室实验和田野实验等直接测量方式，也有通过市场价格反推出投资者隐含信念的间接方法。你的研究中也曾使用过来自不同国家、不同市场的数据。面对如此多样的样本来源和测量方法，在开展研究时，你通常会如何选择和权衡不同的度量方式？你会如何判断某一种测量方法是否能够更准确地捕捉你所关注的信念机制？
Beyond the theoretical mechanisms themselves, measurement at the empirical level is equally important. Take beliefs as an example. Researchers now have a wide range of approaches for measuring them. Some rely on direct measures, such as surveys, laboratory experiments, and field experiments, while others infer investors’ beliefs indirectly from market prices and observed behavior. In your own work, you have also drawn on data from different countries and different financial markets. Given the diversity of both data sources and measurement strategies, how do you typically decide which approach is most appropriate for a particular research question? More specifically, how do you evaluate whether a given measure is actually capturing the belief mechanism you are interested in, rather than something else?
我个人认为，这恰恰是当前这一研究领域面临的一个重要问题。你刚才提到了“偏差合集（bias zoo）”，但我觉得类似的问题不仅存在于因子研究中，在某种程度上，信念研究也出现了“信念合集（belief zoo）”的现象。
I personally think this is actually one of the important challenges facing the field today. You mentioned the idea of a “bias zoo” earlier, but I would argue that a similar issue extends beyond factor research. To some extent, we are also beginning to see a “belief zoo” emerging in the study of beliefs.
在关于信念的研究中，目前存在大量不同的测量方法。研究者可以通过问卷调查直接测量个体的主观信念，也可以利用市场价格信息推断市场中的隐含信念。除此之外，不同研究所关注的对象也存在很大差异：有些研究关注投资者对未来收益的预期，有些关注对公司基本面的预期；有些研究针对个人投资者（retail investors），有些研究关注机构投资者（institutional investors），还有一些研究考察卖方分析师（sell-side analysts）。当这些不同维度同时存在时，研究文献中自然会产生大量不同的发现。但问题在于，许多结论往往具有较强的样本依赖性。不同的测量方法、研究对象以及市场环境，都可能导致不同的研究结果。从更宏观的角度来看，一个研究领域始终需要在两个方向之间寻找平衡：不断提出新的解释、拓展研究边界的同时，也需要在适当阶段对已有研究进行系统整合。
In the study of beliefs, there are currently a wide range of different measurement approaches. Researchers can directly measure individuals’ subjective beliefs through surveys, laboratory experiments, and field experiments. Alternatively, they can infer investors’ underlying beliefs indirectly from market prices and other observable outcomes. Beyond measurement methods, there is also substantial heterogeneity in the objects of study. Some research focuses on investors’ expectations about future returns, while other work examines beliefs about firms’ fundamentals. Some studies investigate retail investors, others focus on institutional investors, and still others examine sell-side analysts. When all of these dimensions vary simultaneously, it is natural for the literature to generate a large number of seemingly different findings. The challenge, however, is that many of these conclusions can be highly dependent on the particular sample being studied. Differences in measurement approaches, research populations, and market environments may all contribute to different empirical results. Therefore, from a broader perspective, any research field must continually strike a balance between two forces. Researchers need to keep developing new explanations and expanding the frontier of knowledge. In addition, at the appropriate stage of development, the field also needs to step back and systematically integrate what has already been learned.
以信念研究的发展为例，大约在2014年前后，相关文献主要依赖个人投资者的收益预期数据展开分析。虽然当时也已经存在一些针对其他类型投资者的研究，但个人投资者仍然是这一领域最主要的研究对象。随着研究不断推进，越来越多的数据来源、研究对象和测量方法被引入，也带来了更加丰富的研究发现。但发展到今天，我认为这一领域已经逐渐进入一个需要进一步整合的阶段。从某种意义上说，未来可能需要一篇类似“驯服信念研究（Taming the belief literature）”的综述性工作，对不同研究之间的差异、联系以及潜在矛盾进行系统梳理。
Taking the development of belief research as an example, around 2014, much of the literature was primarily based on data on individual investors’ return expectations. Although there were already some studies examining other types of investors, retail investors remained the dominant focus of research in this area. As the literature continued to develop, researchers began incorporating a much broader range of data sources, research populations, and measurement approaches, which naturally led to a richer set of empirical findings. However, I believe the field has now gradually reached a stage where greater integration is needed.In some sense, what the literature may need next is a review article along the lines of “Taming the belief literature”—a systematic effort to organize the differences, connections, and potential tensions across existing studies.
例如，我的一位同事一直关注一个非常重要的问题：市场信念究竟应该如何与个体主观信念结合起来理解？市场隐含信念和个人主观信念分别适用于哪些研究问题？二者之间又存在怎样的关系？归根结底，当我们研究信念形成机制时，需要回答一个更基础的问题：我们观察到的现象究竟是某一个特定样本、特定市场环境下的结果，还是反映了一种更深层、更普遍的行为机制？ 对于这一问题，目前学界其实还没有形成完全清晰的答案。也正因为如此，当前信念研究的重要任务已经不仅仅是继续发现新的现象，而是进一步厘清不同测量方法、不同研究对象以及不同研究结论之间的内在联系，识别哪些发现具有更广泛的普适性，哪些结果则主要反映特定情境下的行为表现。
For example, one of my colleagues has been thinking deeply about an important question: how should we understand the relationship between market- level beliefs and individuals’ subjective beliefs? What types of research questions are best suited for market-implied beliefs, and what questions are better addressed using measures of individual beliefs? More fundamentally, how are these two types of beliefs connected? Ultimately, when we study the mechanisms behind belief formation, we need to address a more fundamental issue: are the patterns we observe simply the result of a particular sample or a specific market environment, or do they reflect deeper and more general behavioral mechanisms? At this point, the field has not yet reached a fully clear answer. This is precisely why an important task for belief research today is not simply to continue discovering new phenomena, but rather to better understand the connections among different measurement approaches, research populations, and empirical findings. The goal is to identify which findings reflect more generalizable behavioral principles and which results are primarily driven by specific contexts or environments.
Q4：那么，从你自身的研究经验来看，面对不同的信念测量方法和样本来源，你通常会如何进行选择？在具体研究中，你更倾向于在同一篇论文中结合多种度量方式和不同样本，通过交叉验证来增强对某一机制的可信度；还是更倾向于寻找一个具有独特优势、识别策略更加清晰的研究场景，从而对某一问题进行深入分析？
Drawing from your own research experience, how do you typically approach the choice among different belief measures and data sources? In a given project, do you tend to combine multiple measurement approaches and different samples within the same paper, using cross-validation to strengthen the credibility of a proposed mechanism? Or do you instead prefer to identify a research setting with a unique advantage and a cleaner identification strategy, allowing you to study a particular question in greater depth?
我们之前的研究更多关注的是：哪些因素决定了信念的形成。换句话说，我们主要研究个体层面的信念形成机制，因此通常需要利用样本内部的一些特殊特征，来识别影响信念形成的驱动因素。但近年来，文献中讨论的问题已经有所拓展。例如，某一种信念在总体层面究竟是正向预测还是负向预测市场表现，这类问题往往需要跨样本、跨市场进行比较分析。坦率地说，我自己在这一方向上的研究并不算特别多。相比于探讨信念如何影响市场表现、资金流向或资产价格，我过去更多关注的是信念本身是如何形成的。
Our previous work has focused more on understanding what determines the formation of beliefs. In other words, we have primarily studied the mechanisms through which individuals form their beliefs. To do so, we typically rely on specific features within a given sample to identify the factors that drive belief formation. In recent years, however, the questions being asked in the literature have expanded. For example, researchers have become increasingly interested in whether a particular belief, at the aggregate level, positively or negatively predicts market outcomes. Addressing these questions often requires comparisons across different samples and markets. To be honest, I have not worked extensively on this particular direction myself. Compared with studying how beliefs affect market outcomes, capital flows, or asset prices, my own research has focused more on understanding how beliefs are formed in the first place.
我过去的一些研究在一些程度上依靠所使用的数据样本的独特优势，但这类特殊样本也不可避免地存在一定局限。在研究过程中，我们不仅需要充分利用样本优势来识别潜在机制，也需要投入大量精力去理解并处理样本本身可能带来的限制。 当研究者深入了解一个特殊样本之后，往往需要进一步证明研究发现是否具有更广泛的适用性，并将结果与其他问卷调查数据或已有文献中的发现进行比较。在这个过程中，一个非常有意思的现象是：样本中的某些特征可能与已有研究高度一致，但另一些特征却可能并不完全吻合，最终得到的结果有时会与既有文献产生差异。而当这种差异出现时，研究者自然会进一步追问：哪些发现反映的是更加普遍的行为规律？哪些发现则只是特定样本或特定环境下的结果？
Some of my previous research has relied, to some extent, on the unique advantages of the datasets we were able to access. However, these specialized samples inevitably come with their own limitations. When conducting research, we need to not only take advantage of the strengths of a particular sample to identify potential mechanisms, but also devote substantial effort to understanding and addressing the limitations that the sample itself may introduce. Once researchers develop a deep understanding of a unique dataset or setting, they often need to take the next step and ask whether the findings can be generalized beyond that specific context. This typically involves comparing the results with evidence from other survey datasets or with findings documented in the existing literature. What makes this process particularly interesting is that some features of a given sample may align closely with previous research, while others may differ in important ways. As a result, the findings may sometimes depart from what has been established in the literature. When such differences emerge, researchers naturally begin to ask a deeper question: which findings reflect more general behavioral patterns, and which are primarily driven by a particular sample or institutional environment?
例如，在我们的研究中，个人投资者和机构投资者的某些行为模式实际上表现出了较高的一致性。同时，我们样本中的个人投资者与其他研究中的个人投资者也具有较强的相似性，我们样本中的机构投资者与已有文献中的机构投资者同样大体一致。但另一方面，如果从整个文献体系来看，许多研究又强调个人投资者和机构投资者之间存在显著差异。这就引出了一个更根本的问题：我们真正识别到的究竟是什么？我们观察到的是一种更深层、更普遍的行为机制，还是某一个特定样本环境下形成的经验现象？
For example, in our research, we find that some behavioral patterns among retail investors and institutional investors are actually quite similar. At the same time, the retail investors in our sample also share many characteristics with those studied in previous research, and our institutional investors likewise appear broadly consistent with institutional investors documented in the existing literature. However, when we look at the broader body of research, many studies have emphasized substantial differences between retail and institutional investors. This brings us to a more fundamental question: what exactly are we identifying? Are we uncovering a deeper and more general behavioral mechanism, or are we simply documenting an empirical pattern that emerges within a particular sample or institutional setting?
坦率地说，这也是我目前仍然在努力理解的问题。从某种意义上讲，这正是当前信念研究面临的核心挑战之一。我们正在越来越深入地识别不同样本中的具体机制，但如何判断这些机制具有多大程度的普适性，以及它们能否跨越不同市场环境和投资者群体成立，仍然是未来研究需要进一步解决的问题。
To be honest, this is still a question that I am trying to better understand m-self. In many ways, I think this represents one of the central challenges facing belief research today. We are becoming increasingly effective at identifying specific mechanisms within different samples, but determining the extent to which these mechanisms are broadly applicable—and whether they continue to hold across different market environments and investor populations—remains an important question for future research.
Q5：我们继续延伸刚才的话题。比如，当一篇论文的研究发现与现有文献中的一些普遍性结论并不完全一致时，这是否会在审稿过程中带来额外的挑战？另外，你之前也曾利用中国市场的数据和研究场景开展相关研究。在国际期刊审稿过程中，来自不同市场环境的数据是否会引发审稿人对于外部有效性或普适性的关注？对于这类问题，你有没有一些经验或体会可以与我们分享？
Let me continue with the point we were just discussing. For example, when a paper’s findings do not fully align with some of the established conclusions in the existing literature, does that create additional challenges during the review process? Also, in your previous work, you have used data and research settings from the Chinese market. When submitting to international journals, do findings based on a different market environment raise concerns among reviewers regarding external validity or generalizability? Based on your own experience, are there any lessons or insights you could share about how to address these concerns?
我觉得在这方面，我其实有比较丰富的经验，因为既有成功的经历，也有一些并不那么顺利的经历。我认为，这个问题很大程度上取决于你研究的问题是什么，以及这篇论文本身的定位是什么。
I would say that I have actually gained quite a bit of experience in this area, because I have had both successful experiences and some that were less straightforward.In my view, how reviewers respond to these issues depends largely on the research question being studied and on how the paper itself is positioned.
我最开始有不少研究使用中国数据。例如，我的劳动力市场论文（job market paper）就是利用中国股市的数据来研究中国市场中的相关现象。一方面，研究者对于中国股市的大幅波动、快速上涨以及泡沫现象本身就具有较强兴趣。即使这一现象并非发生在美国或欧洲市场，只要它展现出了足够重要的经济现象和研究价值，学界依然会关注。因此，我认为这一点本身并不是问题。另一方面，虽然这是一篇实证研究，但我们背后有一个相对普适的理论框架来理解泡沫形成机制，然后利用中国市场中的一个具体案例对这一理论进行检验。这样的研究定位其实是比较自然的，因为最终要回答的是一个更一般的问题，而中国市场只是提供了一个具有代表性的研究场景。 我们也明确认识到，具体市场环境与理论框架之间可能存在一定差异。在这篇论文的发表过程中，我并没有经常遇到关于外部有效性的质疑。
Many of my early papers used data from China. For example, my job market paper used data from the Chinese stock market to study a particular phenomenon in that market. On the one hand, researchers are interested in large market fluctuations, rapid price increases, and bubble episodes in China’s stock market. Even if such phenomena do not occur in the U.S. or European markets, as long as they represent economically important phenomena with meaningful research implications, they can still attract attention from the broader academic community. Therefore, I do not think the fact that the data come from China is, by itself, a fundamental concern. On the other hand, although the paper is empirical in nature, it is grounded in a relatively general theoretical framework for understanding the formation of bubbles. We then use a specific episode from the Chinese market as a setting in which to test that theory. I think this is a fairly natural way to position the paper, because the ultimate goal is to answer a broader question, while the Chinese market simply provides a particularly useful and representative research setting. At the same time, we were fully aware that there could be differences between the specific market environment and the theoretical framework. As a result, during the publication process, concerns about external validity were not something I encountered very frequently.
但我的另一篇关于分级基金的论文则有所不同。2015 年前后，分级基金在中国市场大规模兴起，我们围绕这一制度背景研究了一个更具体的问题：当资产结构变得更加复杂时，会如何影响投资者收益、市场表现以及福利分配？换句话说，当金融产品变得更加复杂、多层化和多样化时，是否可能导致投资者之间出现财富转移？这篇论文在审稿过程中确实遇到了较多关于外部有效性的质疑。现在回过头来看，我认为这些质疑其实具有一定合理性。因为分级基金这一产品并不是普遍存在于所有市场，它具有非常具体的制度背景和市场特征。我们不能因为这一类产品在某一时期产生了某种结果，就直接将这一结论推广到所有金融产品复杂化的情境中。而且，问题不仅在于分级基金本身具有特殊性，它还发生在2015年这样一个非常特殊的市场环境中。换句话说，这项研究同时具有三个层面的特殊性：特殊的国家背景、特殊的金融产品以及特殊的时间节点。如果最后希望通过一个高度一般化的理论框架解释这些结果，那么外部有效性问题自然会更加突出。从个人角度来看，这段经历也是非常有价值的学习过程。我现在回头看，仍然很庆幸自己做过这篇研究，因为它让我对这个市场有了更深入的理解，而且直到今天，我仍然认为这是一个非常有意思的研究问题。
However, my paper on structured funds was quite different in this regard. Around 2015, structured funds emerged on a large scale in the Chinese market. In that paper, we used this institutional setting to study a more specific question: when financial products become more complex, how does this complexity affect investor returns, market outcomes, and the distribution of welfare? Put differently, when financial products become more complex, layered, and heterogeneous, can they create wealth transfers among investors? During the review process, this paper did receive substantially more questions and concerns regarding external validity. Looking back, I think many of those concerns were quite reasonable. The reason is that structured funds are not a product category that exists universally across markets; rather, they emerged from a very specific institutional and market environment. We cannot simply observe a particular outcome associated with this type of product in one period and then generalize that conclusion to all situations involving financial product complexity. Moreover, the issue was not only that the product itself was unusual, but also that it emerged during a very distinctive market episode in 2015. In other words, the study involved three layers of specificity: a specific country context, a specific financial product, and a specific point in time. If one ultimately wants to use such a setting to speak to a highly general theoretical framework, concerns about external validity naturally become more prominent. From my own perspective, however, this experience was extremely valuable. Looking back, I am still very glad that I conducted this research, because it gave me a much deeper understanding of this market. Even today, I continue to think that it is a very interesting and important research question.
我觉得，一个数据集具有很多独特特征，或者一个研究发生在一个非常特殊、非常有趣的场景中，并不意味着它在论文写作和发表过程中一定更容易。事实上，有时候研究越具体，其潜在学术受众反而可能越有限。回到刚才提到的分级基金研究，这篇论文最终发表在Review of Finance上，也是一本非常好的期刊。但我个人认为，如果类似现象发生在美国市场，可能在学术传播过程中会获得不同程度的关注。
I think having a dataset with many unique features, or conducting research in a highly specific and interesting setting, does not necessarily make a paper easier to publish. In fact, the more context-specific a study is, the narrower its potential academic audience may become. Going back to the structured funds paper we discussed earlier, the paper was eventually published in the Review of Finance, which is a very good journal. However, my personal view is that if a similar phenomenon had occurred in the U.S. market, it might have attracted a different level of attention during the process of academic dissemination.
学术发表过程中确实可能存在一定程度的地域因素，因为审稿人对于某些市场的制度背景、历史环境和经济意义可能更加熟悉，而对于另一些市场则相对陌生。例如，后来关于游戏驿站（GameStop）的许多研究最终发表在了非常好的期刊上。但与此同时，我们也需要思考：这些研究中的许多结论，是否能够直接推广到中国市场或者欧洲市场？答案未必是肯定的。学术论文的审稿过程不仅取决于研究设计和理论贡献，也不可避免地会受到研究场景的地域特征、审稿人的关注方向以及其自身经验背景等因素影响。
There may indeed be some degree of geographic or contextual bias in academic publishing. Reviewers may be more familiar with the institutional background, historical context, and economic significance of certain markets, while being less familiar with others. For example, many studies on GameStop were eventually published in highly regarded journals. At the same time, however, we should also ask whether many of the conclusions from those studies can be directly generalized to the Chinese or European markets. The answer is not necessarily yes. The review process for academic research depends not only on research design and theoretical contribution, but is also inevitably influenced by factors such as the geographic characteristics of the research setting, the interests and perspectives of reviewers, and their own backgrounds and experiences.
Q6：我正好想到你刚才提到的这个问题。比如，当我们在中国背景下开展研究，并试图与国际主流学术界进行对话时，审稿人有时可能会认为这一研究场景距离他们较远，这对于论文发表未必一定有利。另一方面，我也经常思考，中国市场和社会环境中的一些特征，与西方国家的制度背景和社会环境并不完全相同。由于当前国际经济学和金融学研究长期以来主要在西方学术体系中发展，我们在开展研究时，往往需要将中国经验放入更广泛的理论框架中进行讨论，使其能够与现有文献形成有效对话。
因此，展望未来十年甚至二十年，在推动亚洲研究、中国研究，以及更广泛的非西方市场研究方面，你认为研究者可以做些什么？我们应该如何开展更有解释力的研究，使其不仅能够进入国际学术讨论，也能够更深入地帮助我们理解亚洲和中国自身的发展经验与独特现象？
This actually connects very naturally to the issue you just mentioned. For example, when we conduct research in the Chinese context and try to engage with the international academic community, reviewers may sometimes perceive the research setting as relatively distant from their own experience. This can potentially create additional challenges for publication. At the same time, I often think about the fact that some characteristics of the Chinese market and social environment are not entirely comparable to those of Western countries in terms of institutional background and social structure. Since much of modern economics and finance has historically developed within Western academic systems, researchers studying China or other non-Western contexts often need to place these experiences within broader theoretical frameworks, so that they can engage meaningfully with the existing literature.
Looking ahead over the next decade or two, particularly in promoting research on Asia, China, and more broadly non-Western markets, what do you think researchers can do? How can we conduct research that provides deeper explanatory power—not only allowing these studies to become part of international academic conversations, but also helping us better understand the unique development experiences and phenomena of Asia and China themselves?
说实话，这个问题我还真没想过。因为过去几年，我做得更多的确实像你刚才说的那样：拿一个中国场景，用西方的视角去定位，把它呈现为一个更符合他们审美框架的研究。 对我来说，这个过程不一定是最简单的，因为总会遇到很多类似的情况。我记得有一次在研讨会上，我说我想研究中国投资者的记忆如何影响信念。结果有学者直接说，中国投资者很奇怪，特别喜欢数字8，又特别不喜欢数字4。我当时其实很震惊。后来也遇到过一些类似的评论。当时我就在想，为什么会有这样的评论，我觉得这种判断非常随意。当然，你也可以反驳说，这个问题本身就值得研究，或者进一步讨论这个问题本身的意义。但最后还是要落脚到一点：你得让别人觉得，这个研究代表的不只是一个非常特殊的群体，而是能够反映更广泛的人群。
To be honest, this is not something I have thought about very deeply before. In the past few years, my own research has indeed followed the approach you just described to some extent: taking a Chinese setting and positioning it from a more Western perspective, framing the research in a way that fits more naturally within the existing academic framework. For me, this process has not always been straightforward, because I have encountered many situations like this. I remember once at a seminar, I mentioned that I wanted to study how the memories of Chinese investors affect their beliefs. One scholar immediately responded by saying that Chinese investors are quite unusual—they particularly like the number eight and dislike the number four. I was actually quite shocked by that comment. I have encountered similar reactions on other occasions. At the time, I found myself wondering why people would make such judgments, because I felt that this type of characterization was rather arbitrary. Of course, one could argue that these kinds of cultural features may themselves be interesting research questions, and one could further examine whether they have meaningful implications. But ultimately, the key issue is this: researchers need to convince others that the phenomenon being studied does not represent only a very specific group, but instead reflects patterns that are relevant for a much broader population.
可能在美国，你从来不会遇到这样的问题。没有人会问，为什么要研究美国投资者，或者为什么要对美国投资者感兴趣。也不会有人说，美国投资者之所以值得研究，是因为他们代表了其他市场上的投资者。大家默认美国本身就是一个重要市场、一个重要经济体。但对于中国研究来说，最后还是需要落脚到内容的普适性。在这个过程中，就会出现很多奇奇怪怪的问题。
Perhaps in the United States, researchers never encounter this kind of question. No one would ask why it is important to study U.S. investors or why U.S. investors are worth paying attention to. Nor would people argue that U.S. investors are valuable to study only because they represent investors in other markets. There is an implicit recognition that the United States itself is an important market and a major economy. However, when it comes to research on China, the discussion often still needs to return to the broader applicability of the findings. And in that process, many strange questions can arise.
所以我觉得，这几年我做得更多的是一个沟通者的工作：如何让外国学者在审稿的时候认可这样的数据，同时能够从中国的数据中获得一些具有普适性的见解。至于那些具有中国特征的内容，如何让他们真正认可，或者真正理解，我觉得这一点我还真没有仔细想过。我现在能做的，或者说过去做得更多的，还是在研究和学术交流的过程中，把这种语言铺平，让他们在看待中国的时候，能够用他们熟悉的方式去理解它。 但如果说，要让他们真正像中国人一样看待中国，或者从一个非西方人的视角去理解中国，我也不知道应该怎么做。我觉得如果我能够解决这个问题，学术圈的生态可能会友好很多。
So I think that, in recent years, much of what I have been doing is essentially serving as a bridge or a communicator: trying to help international scholars appreciate the value of data from China during the review process, while also showing them how these data can generate insights that are broadly applicable. As for the aspects that are more uniquely Chinese, I have to admit that I have not thought very deeply about how to make those features truly accepted or fully understood by others. What I have been able to do—or what I have done more often in the past—is to make the language and framing more accessible through research and academic communication, so that when people look at China, they can understand it through concepts and frameworks that they are already familiar with. But if the goal is to help others truly see China in the way Chinese people see it, or to understand China from a perspective that is not primarily Western, I honestly do not know exactly how to achieve that. I think if I were able to solve this problem, the academic environment would become much more inclusive and welcoming.
Q7：首先，我认为应该加强不同文化和学术体系之间的沟通。亚洲文化和欧美文化虽然存在一定差异，但我们本身就需要不断增进彼此之间的理解。其实，这与亚洲学者长期以来努力理解西方社会的过程是类似的，因为我们需要进入他们的学术语境，与他们展开对话，并推动我们的研究被更广泛地认识。但另一方面，我也认为，欧美学者对于中国社会和市场环境的理解仍然有进一步深化的空间。有时候，仅仅基于一些较为表层的认识，研究者可能会将已有的印象或预设带入学术讨论、研讨会交流，甚至体现在审稿意见之中。
Firstly, I think we need to strengthen communication and exchange across different cultural and academic systems. Although Asian cultures and Western cultures differ in many ways, it is important for us to continue building mutual understanding. In many ways, this process is similar to what Asian scholars have been doing for a long time in trying to understand Western societies: we need to enter their academic conversations, engage with their intellectual frameworks, and make our research more widely recognized. At the same time, I also believe that scholars in Europe and the United States still have room to develop a deeper understanding of Chinese society and market environments. Sometimes, based on only a relatively superficial understanding, researchers may bring pre-existing impressions or assumptions into academic discussions, seminar conversations, and even the review process.
当然，这个问题我自己也一直在思考，只是确实还没有完全想清楚。可能一方面，我们仍然需要与西方学者保持持续、深入的学术交流；另一方面，也需要更多地开展针对自身社会和现实环境的深入研究，理解这些现象背后的制度、文化和历史因素。总体来说，从信念形成的角度来看，很多行为和认知过程其实都受到文化和制度环境非常深刻的影响，对吧？
Of course, this is also something that I have been thinking about myself, although I have to admit that I have not yet fully figured it out. Perhaps, on the one hand, we still need to maintain continuous and in-depth academic exchanges with Western scholars. On the other hand, we also need to conduct more systematic research on our own social and institutional environments, in order to better understand the institutional, cultural, and historical factors underlying these phenomena. More broadly, when we think about belief formation, many behavioral and cognitive processes are deeply shaped by cultural and institutional environments, right?
非常同意。我这么说可能听起来有一点像是在强调自己的观点，但不管怎样，我平时确实会和一些非中国学者，或者来自欧洲、美国的学者分享一个想法：如果有机会，真的可以到中国去看一看。很多时候，他们最初未必是从研究的角度出发，但当他们真正来到这里，看到这个社会的发展状态，看到它有自己独特的运行逻辑和社会秩序时，可能会发现，第一手经验比二手印象更可靠，以及不同于他们原有认知的社会运行方式。
I completely agree. What I am about to say may sound a little like I am emphasizing my own perspective, but I do often share this thought with non- Chinese scholars, including researchers from Europe and the United States: if they have the opportunity, they should really consider visiting China and experiencing it firsthand. In many cases, they may not initially approach China from a research perspective. However, once they actually come here and observe how the society has developed, how it operates, and how it has its own unique logic and social order, they may realize that firsthand experience is more reliable than secondhand impressions.and a way of organizing society that differs from what they may have previously assumed.
比如，我一直建议我的一位同事，如果有机会，我们应该在上海生活一周，或者在香港停留两周，亲身观察这个社会，了解这里的社会究竟是如何运行的。因为很多时候，当我们仅仅从学术层面讨论这些问题时，讨论本身可能容易被认为带有较强的立场色彩。但如果你能够真正生活在这里一段时间，深入到具体的日常环境中，不只是作为一个短暂停留的游客，而是真正沉下心去体验这里的便利性，以及社会规范所塑造出的生活方式和社会氛围，你可能会逐渐理解并欣赏这个社会，也会进一步理解和欣赏由这一社会环境所产生的一些研究问题。
For example, I have always suggested to one of my colleagues that, if there is an opportunity, we should spend a week living in Shanghai or perhaps two weeks in Hong Kong, simply to observe firsthand how the society actually functions. Because many times, when we discuss these issues purely at an academic level, the discussion itself can easily be perceived as being shaped by particular positions or perspectives. However, if you actually live in the environment for a period of time and engage with everyday life—not simply as a short-term tourist, but by truly immersing yourself in the local context—you may begin to experience the convenience of daily life, as well as the ways in which social norms shape people’s behaviors, lifestyles, and the broader social atmosphere. Through that kind of experience, you may gradually develop a deeper understanding of and appreciation for the society itself, and also gain a better understanding of the research questions and phenomena that emerge from that social environment.
所以我觉得，像CICF、ABFER这样的学术会议，其实具有非常重要的意义。它们不仅能够促进学术交流，也能够让学者有机会来到不同的社会环境中，亲身感受一个社会是如何运行的，并进一步理解其中的制度和文化机制。即使在正式的学术讨论之外，这种面对面的交流和真实的社会体验本身，也是在促进不同文化和学术体系之间的沟通。
So I think academic conferences such as CICF and ABFER are extremely important in this regard. They not only facilitate academic exchange, but also provide scholars with opportunities to visit different social environments, experience firsthand how societies function, and develop a deeper understanding of the institutional and cultural mechanisms behind them.Even beyond the formal academic discussions, these face-to-face interactions and genuine experiences of different social contexts themselves play an important role in bridging different cultures and academic traditions.
Q8：从刚才的讨论中，你提到了记忆偏差（memory bias）和经历偏差（experience bias）。但我感觉，这两个概念在实际研究中其实很难完全区分。类似地，投射偏差（projection bias）和显著性偏差（salience bias）等概念，很多时候似乎也存在一定程度的重叠。目前来看，我还没有看到现有文献对这些概念之间的区别和边界进行非常清晰的划分。因此，我想请教一下，对于认知经济学中这些相互关联、彼此交叉的概念，你是如何理解的？从研究角度来看，我们应该如何看待这些概念之间的关系？未来的研究又应该如何进一步识别它们各自独立的作用机制，并明确不同认知机制之间的边界？
One issue that naturally follows from our previous discussion concerns the distinction between different cognitive mechanisms. You mentioned memory bias and experience bias earlier, but I feel that in empirical research, it is often difficult to clearly separate these two concepts. Similarly, concepts such as projection bias and salience bias also seem to overlap to some extent. At present, I have not seen the literature provide a very clear framework for distinguishing the boundaries between these related concepts. Therefore, I would like to ask how you think about these interconnected concepts in cognitive economics. From a research perspective, how should we understand the relationship among these mechanisms? Going forward, how can researchers better identify the independent role of each cognitive mechanism and establish clearer boundaries between different underlying processes?
我觉得这个问题非常好。很多时候，我们面临的困惑其实来自两个层面：第一是概念标签本身的问题，第二是现有文献如何进行整合的问题。
I think this is a very good question. In many cases, the challenges we face actually come from two different sources. The first is the issue of the labels themselves—the concepts and terminology we use to describe these mechanisms. The second is the broader question of how the existing literature can be organized and integrated.
从某种意义上来说，经历（experience）和记忆（memory）其实可以被视为高度相关的概念，甚至可以看作同一个过程的不同表述。经历最终会转化为记忆。只不过，在学术讨论中，我们通常会使用“经历效应”这一概念，更多是在延续某篇具体论文对于经历作用的定义和理解。而后续研究可能会从不同角度处理这一形成机制，这也就回到了你刚才提到的问题：究竟哪一种机制更重要？但从本质上来说，经历和记忆之间的联系非常紧密。甚至可以说，很多经济行为最终都与记忆有关，因为我们所经历的一切都已经发生在过去，并以某种形式被储存在我们的认知系统中。从这个意义上讲，它们之间的边界本身并不是非常清晰。
In some sense, experience and memory are actually highly related concepts. They can even be viewed as different ways of describing essentially the same underlying process. Experiences are ultimately transformed into memories. However, in academic discussions, we often use the term “experience effects” because we are following the definition and interpretation of how experiences matter in a particular paper or research tradition. Subsequent studies may approach this underlying formation process from different perspectives, which brings us back to the question you raised earlier: which mechanism is ultimately more important? But fundamentally, the connection between experience and memory is extremely close. One could even argue that many economic behaviors are ultimately related to memory, because everything we experience has already occurred in the past and is stored in some form within our cognitive system. From this perspective, the boundary between experience and memory is itself not always very clear.
当我们尝试区分这些概念时，很多时候并不是在严格意义上区分两个完全独立的机制，而是在将不同研究归入某一类模型或理论框架之下，再与另一类模型或框架进行比较。在这个过程中，我觉得早期研究者当然承担了一部分责任。但更多时候，问题在于我们没有将这些概念放入一个足够清晰的理论框架中进行阐述，从而导致后来的读者在理解时产生困惑，也容易让审稿人在概念界定上提出疑问。因此，我们需要把这些问题明确说明：概念的边界在哪里？不同机制之间的区分标准是什么？从这个角度来看，我认为清晰的定义仍然是一种非常重要且实用的方法。
When we try to distinguish between these concepts, we are often not necessarily separating two completely independent mechanisms in a strict sense. Rather, we are grouping different studies into particular classes of models or theoretical frameworks, and then comparing them with another set of models or frameworks. In this process, I think early researchers certainly bear some responsibility. However, more often than not, the issue is that we have not placed these concepts within sufficiently clear theoretical frameworks. As a result, later readers may become confused when interpreting the literature, and reviewers may also raise questions about how these concepts are defined and distinguished. Therefore, we need to make these issues explicit: Where are the boundaries between different concepts? What criteria should we use to distinguish one mechanism from another? From this perspective, I believe that having clear definitions remains a very important and practical approach.
如果是我们自己撰写论文，也一定需要把这些内容解释清楚。当读者已经对某个概念产生疑问时，作为作者就有责任进一步澄清，而不能简单地将解释责任推给已有文献，只告诉审稿人“这个概念来自哪篇论文”。这远远不够。作者首先需要自己明确：我使用这个概念时具体指什么？在我的研究框架中，什么是经历效应，什么是记忆效应？这种概念界定的责任应该由作者承担，而不是依赖于前人的论文。尤其对于青年学者和博士生而言，更应该通过自己的写作，把理论概念和研究边界阐述清楚。 因为审稿人未必一定是这一具体领域最熟悉的人。很多时候，作者才是最了解自己研究问题和相关文献脉络的人。当然，审稿人的角色并不是比作者更加了解这个问题，而是站在一个独立的、非作者的视角下，判断这篇论文是否能够有效地向读者传递自己的观点。 如果连审稿人都无法理解作者究竟想表达什么，很多时候并不一定意味着审稿人没有理解，而可能意味着作者还没有把自己的问题阐述清楚。
When we write papers ourselves, we also need to explain these issues clearly. Once readers begin to have questions about a particular concept, it is the author’s responsibility to provide further clarification rather than simply shifting the burden of explanation to the existing literature by telling reviewers, “This concept comes from a particular paper. ” That is far from sufficient. Authors first need to be clear about what exactly they mean when they use a concept. Within the framework of their own research, what constitutes an experience effect, and what constitutes a memory effect? Defining these concepts and establishing their boundaries is ultimately the responsibility of the authors themselves, rather than something that can simply be delegated to previous studies. This is especially important for young scholars and PhD students. Through their writing, they need to clearly articulate their theoretical concepts and the boundaries of their research. After all, reviewers are not necessarily the people who know every detail of a specific research area best. In many cases, the authors themselves are the ones who understand their research questions and the relevant literature most deeply. Of course, the role of reviewers is not to know the topic better than the authors. Rather, reviewers provide an independent, outside perspective and evaluate whether the paper successfully communicates its ideas to the broader audience. If reviewers cannot understand what the authors are trying to convey, it does not necessarily mean that the reviewers have failed to understand the paper. In many cases, it may indicate that the authors have not yet articulated their ideas clearly enough.
我对这个问题也有比较深的感触。因为你刚才提到的经历和记忆，其实类似的问题几乎可以延伸到很多研究领域。我完全可以将同一个模型称为“经历效应模型”，也可以将其称为“记忆模型”，反过来也同样成立。实际上，当研究者使用这些概念时，很多时候指的并不是某一个严格定义、完全独立的机制，而是在引用某篇具体论文中提出的某一种模型或研究框架。在理解这些概念时，我们不能只关注名称本身，而需要回到具体的文献背景、理论框架以及研究语境之中。 只有这样，才能真正理解这些概念背后的含义，以及不同研究之间到底存在怎样的联系和区别。
I have also thought quite deeply about this issue. The problem you just mentioned regarding experience and memory can actually be extended to many other areas of research. For example, the same model could be described as an “experience effects model, ” but it could also be referred to as a “memory model, ” and the reverse could also be true. In reality, when researchers use these concepts, they often do not necessarily refer to a single, strictly defined, and completely independent mechanism. Rather, they are often referring to a particular model or research framework introduced in a specific paper or literature tradition. Therefore, when trying to understand these concepts, we cannot focus only on the labels themselves. Instead, we need to return to the specific literature background, theoretical framework, and research context in which these concepts are used. Only in this way can we truly understand what these concepts mean, as well as the connections and distinctions that exist across different studies.
Q9：我的问题可能会更偏向行为经济学和创业研究一些。你刚才提到了过度自信（overconfidence），而我自己在研究创业问题时，也发现这一领域存在很多交叉之处。比如，创业者的投资决策往往与其信念形成过程密切相关。我在研究中发现，创业者进行第二次创业的一个重要原因，可能来自第一次创业经历中的成功反馈，而这种成功经验又可能进一步强化创业者的过度自信，并影响其后续决策。
所以我有两个问题。第一个问题是，关于过度自信以及相关信念形成机制，在管理学，尤其是创业研究领域，已经有相当丰富的讨论；但相比之下，在经济学框架下的系统研究似乎相对较少。第二个问题是，当你开展行为经济学或金融学研究，并向综合类顶级期刊投稿时，审稿人的背景通常主要来自金融学领域，还是也会包括经济学领域的研究者？
My question is perhaps more related to behavioral economics and entrepreneurship research. You mentioned overconfidence earlier, and in my own research on entrepreneurship, I have also found many interesting connections with this area. For example, entrepreneurs’ investment decisions are often closely related to how their beliefs are formed. In my research, I have found that one important reason why entrepreneurs start a second venture may come from the positive feedback generated by the success of their first venture. Such successful experiences may further reinforce entrepreneurs’ overconfidence and subsequently influence their future decisions.
So I have two questions. First, regarding overconfidence and related belief formation mechanisms, there has already been a substantial body of research in management, particularly in the entrepreneurship literature. However, compared with this literature, systematic research within the economics framework appears to be relatively more limited. My second question is about the review process. When you conduct research in behavioral economics or finance and submit papers to broad-scope top journals, are the reviewers typically drawn primarily from the finance field, or do they also include researchers from economics and related disciplines?
我先回答第二个问题。综合来看，审稿人一般还是来自经济学领域，真正遇到金融学背景审稿人的情况其实并不算多。
Let me answer your second question first. Overall, reviewers for broad- scope journals are generally drawn from the economics field. In my experience, it is actually not that common to have reviewers who primarily come from a finance background.
我刚才提到的那两篇文章，一篇更偏向金融学研究，另一篇则更加接近纯粹的行为经济学研究。只不过，我的两位合作者主要从事行为经济学研究，而我的研究背景更多是行为金融。因此，从我的个人经验来看，在面对经济学审稿人的过程中，失败的经验可能比成功的经验更多。我觉得经济学审稿人的要求确实更严格，评价标准也更高。
The two papers I mentioned earlier actually represent two somewhat different types of research. One is more closely related to finance, while the other is closer to a pure behavioral economics study. However, my two coauthors mainly work in behavioral economics, whereas my own background is more in behavioral finance. So, based on my personal experience, when dealing with economics reviewers, I had more failures than successes. I do think that reviewers in economics are indeed stricter than those in finance and often evaluate papers according to particularly demanding criteria.
再回到第一个问题。我觉得你提到的创业场景非常有意思。至少从我观察身边朋友的经历来看，创业者最开始获得的成功，比如赚到第一桶金，当然可能与个人能力有关，但其中也往往包含一定的运气成分。问题在于：当成功发生之后，人们往往会倾向于将结果更多归因于自身能力。因此，我觉得你提出的这个问题非常值得研究，也很容易引起共鸣。真正像埃隆·马斯克这样，能够连续进行创新，并且多次取得成功的案例，其实非常少见。另一方面，过度自信本身也可能是一种具有一定合理性的心理机制。对于创业者而言，你往往需要拥有一种非常坚定的信念：相信自己正在做的事情能够成功，相信自己能够比别人做得更好。从某种意义上说，也许正是因为这种强烈的信念，创业者才愿意投入大量资源和精力，并最终增加成功的可能性。
Going back to your first question, I think the entrepreneurial setting you mentioned is particularly interesting. At least from observing the experiences of people around me, the initial success entrepreneurs achieve — for example, earning their first significant amount of money — may certainly reflect their own ability, but it often also contains an element of luck. The challenge is that once success occurs, people tend to attribute the outcome more heavily to their own abilities. This creates a very interesting research question, and I think it is also highly intuitive and relatable. Truly exceptional cases, such as Elon Musk, who has repeatedly pursued innovation and achieved success across multiple ventures, are actually quite rare. At the same time, overconfidence itself may be a psychologically reasonable mechanism to some extent. For entrepreneurs, it is often necessary to have a strong and unwavering belief that what they are pursuing can succeed and that they can outperform others. In this sense, it may be precisely because of this strong conviction that entrepreneurs are willing to commit substantial resources and effort, which ultimately increases their chances of success.
其实，研究工作也是类似的：你需要相信自己的论文有发表的可能，或者相信自己研究的问题具有重要价值、有足够吸引力，才愿意长期投入时间和精力，并最终把研究完成。 所以，我觉得过度自信中存在一个非常有意思的问题：它是否本质上是一种动机性推理（motivated reasoning）？以及，在某些情况下，它是否能够被理性化？如果一个人的成功部分取决于自身努力，而努力又受到自我认知和信念的影响，那么信念本身就可能改变最终结果。比如，一个人的成功取决于他的努力程度，而他的努力程度又取决于他如何看待自己的能力。在这种情况下，过度自信是否反而可能成为一种促进成功的机制？我觉得，这是一个非常值得进一步研究的问题。
In fact, research itself is quite similar in this regard. You need to believe that your paper has a chance of being published, or that the question you are studying has important value and sufficient appeal, in order to be willing to devote a substantial amount of time and effort to the project and ultimately bring it to completion. So I think one particularly interesting question about overconfidence is whether it is fundamentally a form of motivated reasoning, and whether it can be rationalized under certain circumstances. If an individual’s success depends partly on their own effort, and effort itself is influenced by how they perceive their own ability and prospects, then beliefs can actually affect outcomes. For example, if success depends on how much effort someone puts in, and effort depends on how they evaluate their own ability, then could overconfidence, in some cases, become a mechanism that contributes to success rather than simply a source of bias? I think this is a very interesting question that deserves further research.
Q10：我们公众号的大部分读者仍然是青年学者，如果他们想要从事行为金融领域的研究，有没有什么建议或者提示给大家？
Most of our readers are young scholars. If they are interested in conducting research in behavioral finance, are there any suggestions or advice you would like to share with them?
其实，我当年在个人陈述中就明确写过自己希望研究的问题。读完经历效应（experience effect）的相关文献之后，我当时就在思考：那些经历过历史大事件的人，他们的人生经历是否会对后续的风险承担行为产生长期影响？比如，在终身决策或者生命周期中的各种选择上，这些经历是否会造成系统性的差异？
Actually, when I wrote my personal statement years ago, I had already clearly described the type of questions I wanted to study. After reading the literature on experience effects, I started thinking about a question: Do the life experiences of people who went through major historical events have long-term effects on their subsequent risk-taking behavior? For example, could these experiences lead to systematic differences in decisions over the course of their lives, such as their choices in long-term planning, lifetime decisions, or other important economic decisions?
现在回过头来看，这个问题其实与很多研究主题都有联系。但经过这么多年，我最终仍然在研究与记忆相关的问题。我觉得这个领域确实非常有意思。我一直认为，无论是研究这些现象，还是反思这些问题，都需要我们不断观察外部世界，同时也观察自己。所以，我觉得行为研究最有趣的一点在于，你研究的对象其实在某种程度上也是你自己。 个人经历在研究过程中非常重要。很多时候，研究灵感并不一定来自已有文献，也可能来自对自身经历的反思、对周围环境的观察，以及对日常现象的思考。对我来说，这一直是一个非常有价值的过程。我的好朋友曾经说过，他最大的研究灵感来源是他的女朋友。
Looking back now, this question actually connects to many different research themes. But after all these years, I have ultimately continued to study questions related to memory. I think this area is genuinely fascinating.I have always believed that, whether we are studying these phenomena or reflecting on these questions, we need to constantly observe both the world around us and ourselves. In my view, one of the most interesting aspects of behavioral research is that the subject you study is, in some sense, also yourself. Personal experiences can play a very important role in the research process. Many times, research ideas do not necessarily come only from reading the existing literature. They can also emerge from reflecting on our own experiences, observing the environment around us, and thinking carefully about everyday phenomena. For me, this has always been an extremely valuable process. My good friend once told me that his greatest source of research inspiration comes from his girlfriend.
这些年来，行为金融学一直在不断发展，也不断有新的研究问题和新的研究方法进入这个领域。每年看到新的劳动力市场候选人，我都会发现很多年轻学者仍然在研究这些重要问题，而且其中不少人最终进入了非常优秀的学校和研究机构，持续推动着这个领域的边界向外拓展。从科学发展的角度来看，我对这个领域仍然非常乐观。不同阶段的学者——无论是已经建立领域基础的前辈学者，还是正在成长中的中青年学者，以及刚刚进入领域的年轻研究者——都在从不同角度推动行为金融的发展。 能够身处这样一个不断交流、不断创新的学术共同体中，我确实对这个领域感到非常骄傲。
Over the years, behavioral finance has continued to evolve, with new research questions and new methodologies constantly entering the field. Every year, when I see new candidates on the labor market, I am reminded that many young scholars are still working on these important questions. Many of them eventually join excellent universities and research institutions, continuing to push the boundaries of the field. From the perspective of scientific progress, I remain very optimistic about the future of behavioral finance. Scholars at different stages of their careers — from senior researchers who helped establish the foundations of the field, to mid-career scholars who are continuing to expand its frontiers, and to young researchers who are just entering the field — are all contributing to the development of behavioral finance from different perspectives. Being part of such an academic community, where people continuously exchange ideas and generate new innovations, makes me genuinely proud of this field.
当然，我认为从事学术研究最重要的还是兴趣。 我并不是建议所有人都选择我的研究方向，或者都来做行为金融。记得我当年在耶鲁读书的时候，也曾经听到有人说：“行为金融特别不好找工作。”这是当时一种比较常见的看法。但现在回过头来看，我觉得这种说法并不准确。至少从这些年的发展来看，并不存在所谓“行为金融特别不好找工作”这样的情况。对于年轻研究者来说，更重要的是关注自己是否真正对某一个问题感兴趣，是否愿意长期投入并深入研究。事实上，过去这些年中，也有很多研究行为金融的学者最终获得了非常好的学术机会。我觉得青年学者不必过度担心某一个具体领域的发展前景，更重要的是找到自己真正感兴趣、愿意长期投入的问题。
Of course, I think the most important thing in pursuing academic research is genuine interest. I would not suggest that everyone should follow my research path or choose behavioral finance as their field. I remember when I was a student at Yale, I heard people say that “behavioral finance is a very difficult field for finding academic jobs. ” At the time, this was actually a fairly common perception. But looking back now, I do not think that view was accurate. At least based on how the field has developed over the past several years, there has certainly not been a situation where behavioral finance scholars have been unable to find good academic positions. For young researchers, I think the more important question is whether they are genuinely interested in a particular research question and whether they are willing to devote the time and effort needed to study it deeply over the long term. In fact, many scholars working in behavioral finance have gone on to obtain excellent academic opportunities over the years. So I think young researchers do not need to worry too much about the future prospects of any particular field. What matters more is finding questions that they are truly passionate about and willing to pursue over the long run.
Q11：从头到尾，你其实一直在强调一个核心问题，就是我们这个领域的边界究竟在哪里，对吧？大家也一直在不断探索新的研究方向，同时对已有知识进行整合和总结。所以我觉得，对于青年学者来说，首先理解和厘清已有研究的边界其实非常重要。只有对自己正在从事的研究领域、相关文献以及已有成果有足够深入的认识，才能在此基础上进一步推动研究边界的拓展。
Throughout our conversation, you have actually been emphasizing one central question: where exactly are the boundaries of our field? Researchers are constantly exploring new directions while also trying to integrate and consolidate existing knowledge. So I think, for young scholars, one of the most important first steps is to understand and clarify the boundaries of the existing literature. Only by developing a sufficiently deep understanding of the field they are working in, the relevant literature, and the knowledge that has already been established can researchers build on that foundation and further push the boundaries of research.
回到青年学者的话题上，我每次去亚洲的一些学校时，都会感受到那里有很多非常聪明、也非常有创造力的学生。他们并不是缺乏写论文的能力，而是在一定程度上受到物理距离的影响，对于这个领域最新的研究进展，以及一些已经被广泛讨论过的问题，可能了解得还不够充分。对于青年研究者来说，一个非常重要的能力，是要建立在已有研究基础上，清楚地了解这个领域目前正在讨论什么、已有研究已经解决了哪些问题，然后再从已有文献的边缘位置寻找新的切入点，进一步推动研究的发展。 我觉得，这可能是最困难的部分，同时也体现了学术交流和信息获取本身所存在的成本。
Coming back to the topic of young scholars, whenever I visit universities in Asia, I often find that there are many students who are extremely talented and highly creative. The issue is not that they lack the ability to write papers. Rather, to some extent, they are affected by physical distance and may not have sufficient exposure to the latest developments in the field or to questions that have already been extensively discussed in the literature. For young researchers, one of the most important skills is to build on existing research, develop a clear understanding of what questions the field is currently debating, and recognize which problems have already been addressed. Only then can they identify new opportunities at the frontier of the existing literature and further advance the field.I think this is perhaps one of the most challenging parts of doing research. At the same time, it also reflects the costs associated with academic communication and access to information.
甚至即使是在英国作为一名教师，有时候参加学术会议时，我也会思考：这次会议是否真的值得参加？因为参加会议本身也存在时间和资源成本。对于青年研究者来说，持续跟踪领域最新动态本身就并不容易，更不用说对于身处亚洲某些高校的博士生而言，他们在获取信息、参与学术讨论以及建立学术网络方面，可能面临更高的成本。但我想强调的是，当你能够真正跟进最新的研究动态，了解这个领域正在发生什么，而不是被动地接受已有研究结论，而是进一步进行批判性的评估和思考——例如思考这个领域未来可能的发展方向——那么这个过程本身会带来非常大的收获。
Even as a faculty member in the UK, I sometimes find myself asking whether attending a particular academic conference is truly worthwhile, because participating in conferences also involves costs in terms of time and resources. For young researchers, staying continuously updated with the latest developments in a field is already challenging. For PhD students at universities in parts of Asia, the costs of accessing information, participating in academic discussions, and building academic networks may be even higher. But what I want to emphasize is that once you are able to genuinely keep up with the latest developments in the field and understand what is currently happening in the research frontier, the process can be extremely rewarding. The key is not to passively absorb existing findings, but to critically evaluate and reflect on them — for example, by thinking about where the field might be heading in the future. This process itself can bring tremendous value.
比如今年4月份，我看到一个最新的NBER项目。当时在我们的内部讨论中，我们其实已经开始思考：这一方向未来还可以如何进一步延伸。但如果一个学生并不处于这样的学术交流环境之中，他可能就需要更多依靠自己的判断，去推测这个领域未来可能的发展方向。所以，我觉得，对于青年研究者来说，这确实是一个更大的挑战。但如果你能够持续培养这样的思考方式——不断跟进最新研究动态，判断未来可能的发展方向，并结合正在发表的论文去检验自己的判断——那么你会逐渐形成对于研究方向的判断力，也会越来越清楚一个问题应该如何继续推进。 从这个意义上来说，这其实也是一个非常好的学习过程。
For example, in April this year, I came across a new NBER project. At the time, during our internal discussions, we had already started thinking about how this line of research could potentially be extended in the future. However, if a student is not embedded in an environment with this kind of academic exchange, they may need to rely much more on their own judgment to anticipate where the field might be heading. So I think this is indeed a greater challenge for young researchers. But if you can continuously cultivate this way of thinking — keeping up with the latest developments in the literature, forming your own views about where research directions may evolve, and then testing those views against newly published papers — you will gradually develop the ability to judge promising research directions. Over time, you will also become increasingly clear about how a research question can be further developed and advanced. In this sense, this process itself is a very valuable learning experience.
学者简介：
Cameron Peng is currently an Assistant Professor of Finance at the London School of Economics and Political Science (LSE), Director of the Capital Markets Programme at the Financial Markets Group (FMG), and a Research Affiliate at CEPR. He received his bachelor’s degree in Finance from the Guanghua School of Management at Peking University and obtained his Ph.D. in Financial Economics from Yale University in 2018, where he was supervised by internationally renowned scholars including Nicholas Barberis. His research focuses on asset pricing, behavioral economics, behavioral finance, and household finance. His work explores topics including investor belief biases, memory and decision-making, household investment behavior, and asset complexity, combining theoretical innovation with rigorous empirical analysis.His research has been published in leading international journals, including the Quarterly Journal of Economics, Journal of Financial Economics, Review of Financial Studies, and Econometrica. He has received numerous honors, including the CFRC Best Paper Award, the CFAM-ARX Paper Award, and the Second Prize in the CQA Academic Competition. He has also received multiple LSE Excellence in Education Awards. He has served on the programme committees of major finance conferences, including the European Finance Association (EFA), Financial Intermediation Research Society (FIRS), and Midwest Finance Association (MFA). He has served as a referee for nearly 20 leading academic journals, including Econometrica, the Journal of Finance, and the Review of Financial Studies, and has been actively involved in organizing academic conferences in the field of behavioral finance.
彭程，现任伦敦政治经济学院（LSE）金融学助理教授、金融市场集团（FMG）资本市场项目主任，欧洲经济政策研究中心（CEPR）研究员。本科毕业于北京大学光华管理学院金融学专业，2018 年获耶鲁大学金融经济学博士学位，师从 Nicholas Barberis 等国际知名学者。研究聚焦资产定价、行为经济学、行为金融学与家庭金融，围绕投资者信念偏差、记忆与决策、家庭投资行为、资产复杂性等议题展开，成果兼具理论创新与实证严谨性。多篇论文发表于Quarterly Journal of Economics、Journal of Financial Economics、Review of Financial Studies、Econometrica等国际顶刊，曾获 CFRC 最佳论文奖、CFAM-ARX 论文奖、CQA 学术竞赛二等奖等多项荣誉，并多次荣获 LSE 卓越教学奖。长期担任 EFA、FIRS、MFA 等顶级金融会议程序委员，为Econometrica、Journal of Finance、Review of Financial Studies等近 20 本权威期刊审稿，积极组织行为金融领域学术会议。
参考文献：
[1]Liu, H., Peng, C., Xiong, W. A., & Xiong, W. (2022). Taming the bias zoo. Journal of Financial Economics, 143(2), 716-741.
[2]Fan, T. Q., Liang, Y., & Peng, C. (2024). The inference-forecast gap in belief updating. Econometrica , forthcoming.
[3]Jiang, Z., Liu, H., Peng, C., & Yan, H. (2025). Investor memory and biased beliefs: Evidence from the field. The Quarterly Journal of Economics, 140(4), 2749-2804.
| 责任编辑 | 阮天悦 |
| 整理翻译 | 陈舒婷 |
| 校对 | 彭程 |